Causal Inference: What If
Miguel A. Hern´an, James M. Robins
April 26, 2024
ii Causal Inference
Copyright 2020, 2024 Miguel Hern´an and James Robins
All rights reserved. No portion of this book can be reproduced for publi-
cation without express permission from the copyright holders, except as permit-
ted by U.S. copyright law. For permissions, contact miguel hernan@post.harvard.edu
Cover design by Josh McKible
LaTex design by Roger Logan
Suggested citation: Hern´an MA, Robins JM (2020). Causal Inference:
What If. Boca Raton: Chapman & Hall/CRC.
This book is available online at https://www.hsph.harvard.edu/miguel-
hernan/causal-inference-book/
A print version (for purchase) is expected to become available soon.
Contents
Introduction: Towards less casual causal inferences vii
I Causal inference without models 1
1 A definition of causal effect 3
1.1 Individual causal effects . . . . . . . . . . . . . . . . . . . . . . . 3
1.2 Average causal effects . . . . . . . . . . . . . . . . . . . . . . . . 4
1.3 Measures of causal effect . . . . . . . . . . . . . . . . . . . . . . . 7
1.4 Random variability . . . . . . . . . . . . . . . . . . . . . . . . . . 8
1.5 Causation versus association . . . . . . . . . . . . . . . . . . . . 10
2 Randomized experiments 13
2.1 Randomization . . . . . . . . . . . . . . . . . . . . . . . . . . . . 13
2.2 Conditional randomization . . . . . . . . . . . . . . . . . . . . . 17
2.3 Standardization . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19
2.4 Inverse probability weighting . . . . . . . . . . . . . . . . . . . . 20
3 Observational studies 27
3.1 Identifiability conditions . . . . . . . . . . . . . . . . . . . . . . . 27
3.2 Exchangeability . . . . . . . . . . . . . . . . . . . . . . . . . . . . 29
3.3 Positivity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
3.4 Consistency: First, define the counterfactual outcome . . . . . . 33
3.5 Consistency: Second, link counterfactuals to the observed data . 37
3.6 The target trial . . . . . . . . . . . . . . . . . . . . . . . . . . . . 38
4 Effect modification 43
4.1 Heterogeneity of treatment effects . . . . . . . . . . . . . . . . . 43
4.2 Stratification to identify effect modification . . . . . . . . . . . . 45
4.3 Why care about effect modification . . . . . . . . . . . . . . . . . 47
4.4 Stratification as a form of adjustment . . . . . . . . . . . . . . . 49
4.5 Matching as another form of adjustment . . . . . . . . . . . . . . 51
4.6 Effect modification and adjustment methods . . . . . . . . . . . 52
5 Interaction 57
5.1 Interaction requires a joint intervention . . . . . . . . . . . . . . 57
5.2 Identifying interaction . . . . . . . . . . . . . . . . . . . . . . . . 58
5.3 Counterfactual response types and interaction . . . . . . . . . . . 60
5.4 Sufficient causes . . . . . . . . . . . . . . . . . . . . . . . . . . . 62
5.5 Sufficient cause interaction . . . . . . . . . . . . . . . . . . . . . 65
5.6 Counterfactuals or sufficient-component causes? . . . . . . . . . . 67
iv Causal Inference
6 Graphical representation of causal effects 71
6.1 Causal diagrams . . . . . . . . . . . . . . . . . . . . . . . . . . . 71
6.2 Causal diagrams and marginal independence . . . . . . . . . . . 73
6.3 Causal diagrams and conditional independence . . . . . . . . . . 76
6.4 Positivity and consistency in causal diagrams . . . . . . . . . . . 77
6.5 A structural classification of bias . . . . . . . . . . . . . . . . . . 81
6.6 The structure of effect modification . . . . . . . . . . . . . . . . . 83
7 Confounding 85
7.1 The structure of confounding . . . . . . . . . . . . . . . . . . . . 85
7.2 Confounding and exchangeability . . . . . . . . . . . . . . . . . . 87
7.3 Confounding and the backdoor criterion . . . . . . . . . . . . . . 89
7.4 Confounding and confounders . . . . . . . . . . . . . . . . . . . . 92
7.5 Single-world intervention graphs . . . . . . . . . . . . . . . . . . 95
7.6 Confounding adjustment . . . . . . . . . . . . . . . . . . . . . . . 96
8 Selection bias 103
8.1 The structure of selection bias . . . . . . . . . . . . . . . . . . . 103
8.2 Examples of selection bias . . . . . . . . . . . . . . . . . . . . . . 105
8.3 Selection bias and confounding . . . . . . . . . . . . . . . . . . . 107
8.4 Selection bias and censoring . . . . . . . . . . . . . . . . . . . . . 109
8.5 How to adjust for selection bias . . . . . . . . . . . . . . . . . . . 111
8.6 Selection without bias . . . . . . . . . . . . . . . . . . . . . . . . 115
9 Measurement bias and “Noncausal” diagrams 119
9.1 Measurement error . . . . . . . . . . . . . . . . . . . . . . . . . . 119
9.2 The structure of measurement error . . . . . . . . . . . . . . . . 120
9.3 Mismeasured confounders and colliders . . . . . . . . . . . . . . . 122
9.4 Causal diagrams without mismeasured variables? . . . . . . . . . 124
9.5 Many proposed causal diagrams include noncausal arrows . . . . 125
9.6 Does it matter that many proposed diagrams include noncausal
arrows? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128
10 Random variability 131
10.1 Identification versus estimation . . . . . . . . . . . . . . . . . . 131
10.2 Estimation of causal effects . . . . . . . . . . . . . . . . . . . . 134
10.3 The myth of the super-population . . . . . . . . . . . . . . . . . 136
10.4 The conditionality “principle” . . . . . . . . . . . . . . . . . . . 138
10.5 The curse of dimensionality . . . . . . . . . . . . . . . . . . . . 142
II Causal inference with models 145
11 Why model? 147
11.1 Data cannot speak for themselves . . . . . . . . . . . . . . . . . 147
11.2 Parametric estimators of the conditional mean . . . . . . . . . . 149
11.3 Nonparametric estimators of the conditional mean . . . . . . . 150
11.4 Smoothing . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 151
11.5 The bias-variance trade-off . . . . . . . . . . . . . . . . . . . . . 153
CONTENTS v
12 IP weighting and marginal structural models 157
12.1 The causal question . . . . . . . . . . . . . . . . . . . . . . . . . 157
12.2 Estimating IP weights via modeling . . . . . . . . . . . . . . . . 158
12.3 Stabilized IP weights . . . . . . . . . . . . . . . . . . . . . . . . 161
12.4 Marginal structural models . . . . . . . . . . . . . . . . . . . . . 163
12.5 Effect modification and marginal structural models . . . . . . . 165
12.6 Censoring and missing data . . . . . . . . . . . . . . . . . . . . 166
13 Standardization and the parametric g-formula 169
13.1 Standardization as an alternative to IP weighting . . . . . . . . 169
13.2 Estimating the mean outcome via modeling . . . . . . . . . . . 171
13.3 Standardizing the mean outcome to the confounder distribution 172
13.4 IP weighting or standardization? . . . . . . . . . . . . . . . . . 173
13.5 How seriously do we take our estimates? . . . . . . . . . . . . . 175
14 G-estimation of structural nested models 181
14.1 The causal question revisited . . . . . . . . . . . . . . . . . . . 181
14.2 Exchangeability revisited . . . . . . . . . . . . . . . . . . . . . . 182
14.3 Structural nested mean models . . . . . . . . . . . . . . . . . . 183
14.4 Rank preservation . . . . . . . . . . . . . . . . . . . . . . . . . . 185
14.5 G-estimation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 187
14.6 Structural nested models with two or more parameters . . . . . 190
15 Outcome regression and propensity scores 193
15.1 Outcome regression . . . . . . . . . . . . . . . . . . . . . . . . . 193
15.2 Propensity scores . . . . . . . . . . . . . . . . . . . . . . . . . . 195
15.3 Propensity stratification and standardization . . . . . . . . . . . 196
15.4 Propensity matching . . . . . . . . . . . . . . . . . . . . . . . . 198
15.5 Propensity models, structural models, predictive models . . . . 199
16 Instrumental variable estimation 203
16.1 The three instrumental conditions . . . . . . . . . . . . . . . . . 203
16.2 The usual IV estimand . . . . . . . . . . . . . . . . . . . . . . . 206
16.3 A fourth identifying condition: homogeneity . . . . . . . . . . . 208
16.4 An alternative fourth condition: monotonicity . . . . . . . . . . 211
16.5 The three instrumental conditions revisited . . . . . . . . . . . 214
16.6 Instrumental variable estimation versus other methods . . . . . 217
17 Causal survival analysis 221
17.1 Hazards and risks . . . . . . . . . . . . . . . . . . . . . . . . . . 221
17.2 From hazards to risks . . . . . . . . . . . . . . . . . . . . . . . . 223
17.3 Why censoring matters . . . . . . . . . . . . . . . . . . . . . . . 226
17.4 IP weighting of marginal structural models . . . . . . . . . . . . 228
17.5 The parametric g-formula . . . . . . . . . . . . . . . . . . . . . 230
17.6 G-estimation of structural nested models . . . . . . . . . . . . . 231
18 Variable selection and high-dimensional data 235
18.1 The different goals of variable selection . . . . . . . . . . . . . . 235
18.2 Variables that induce or amplify bias . . . . . . . . . . . . . . . 236
18.3 Causal inference and machine learning . . . . . . . . . . . . . . 240
18.4 Doubly robust machine learning estimators . . . . . . . . . . . . 241
18.5 Variable selection is a difficult problem . . . . . . . . . . . . . . 244
vi Causal Inference
III Causal inference for time-varying treatments 247
19 Time-varying treatments 249
19.1 The causal effect of time-varying treatments . . . . . . . . . . . 249
19.2 Treatment strategies . . . . . . . . . . . . . . . . . . . . . . . . 250
19.3 Sequentially randomized experiments . . . . . . . . . . . . . . . 251
19.4 Sequential exchangeability . . . . . . . . . . . . . . . . . . . . . 253
19.5 Identifiability under some but not all treatment strategies . . . 255
19.6 Time-varying confounding and time-varying confounders . . . . 259
20 Treatment-confounder feedback 261
20.1 The elements of treatment-confounder feedback . . . . . . . . . 261
20.2 The bias of traditional methods . . . . . . . . . . . . . . . . . . 263
20.3 Why traditional methods fail . . . . . . . . . . . . . . . . . . . 265
20.4 Why traditional methods cannot be fixed . . . . . . . . . . . . . 267
20.5 Adjusting for past treatment . . . . . . . . . . . . . . . . . . . . 268
21 G-methods for time-varying treatments 271
21.1 The g-formula for time-varying treatments . . . . . . . . . . . . 271
21.2 IP weighting for time-varying treatments . . . . . . . . . . . . . 276
21.3 A doubly robust estimator for time-varying treatments . . . . . 280
21.4 G-estimation for time-varying treatments . . . . . . . . . . . . . 283
21.5 Censoring is a time-varying treatment . . . . . . . . . . . . . . 291
21.6 The big g-formula . . . . . . . . . . . . . . . . . . . . . . . . . . 294
22 Target trial emulation 299
22.1 Intention-to-treat effect and per-protocol effect . . . . . . . . . 299
22.2 A target trial with sustained treatment strategies . . . . . . . . 303
22.3 Emulating a target trial with sustained strategies . . . . . . . . 307
22.4 Time zero . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 309
22.5 A unified approach to answer What If questions with data . . . 311
23 Causal mediation 317
23.1 Mediation analysis under attack . . . . . . . . . . . . . . . . . . 317
23.2 A defense of mediation analysis . . . . . . . . . . . . . . . . . . 319
23.3 Empirically verifiable mediation . . . . . . . . . . . . . . . . . . 321
23.4 An interventionist theory of mediation . . . . . . . . . . . . . . 323
References 326
Index 345
INTRODUCTION: TOWARDS LESS CASUAL CAUSAL INFERENCES
Causal Inference is an admittedly pretentious title for a book. A complex
scientific task, causal inference relies on triangulating evidence from multiple
sources and on the application of a variety of methodological approaches. No
book can possibly provide a comprehensive description of all methodologies for
causal inference across the sciences. The authors of any Causal Inference book
will have to choose which aspects of causal inference methodology they want
to emphasize.
The title of this introduction reflects our own choices: a book that helps
scientists—especially health and social scientists—generate and analyze data
to make causal inferences that are explicit about both the causal question and
the assumptions underlying the data analysis. Unfortunately, the scientific
literature is plagued by studies in which the causal question is not explicitly
stated and the investigators’ unverifiable assumptions are not declared. This
casual attitude towards causal inference has led to a great deal of confusion.
For example, it is not uncommon to find studies in which the effect estimates
are hard to interpret because the data analysis methods cannot appropriately
answer the causal question (were it explicitly stated) under the investigators’
assumptions (were they declared).
In this book, we stress the need to take the causal question seriously enough
to articulate it, and to delineate the separate roles of data and assumptions for
causal inference. Once these foundations are in place, causal inferences become
necessarily less casual, which helps prevent confusion. The book describes
various data analysis approaches to estimate the causal effect of interest under
a particular set of assumptions when data are collected on each individual in
a population. A key message of the book is that causal inference cannot be
reduced to a collection of recipes for data analysis.
This is not a philosophy book. We remain largely agnostic about metaphys-
ical concepts like causality and cause. Instead, we focus on the identification
and estimation of causal effects in populations, i.e., numerical quantities that
measure changes in the distribution of an outcome under different interven-
tions. For example, we discuss how to estimate the risk of death in patients
with serious heart failure if they received a heart transplant versus if they did
not. Through actionable causal inference, we want to help decision makers
make better decisions.
The book is divided in three parts of increasing difficulty: Part I is about
causal inference without models (i.e., nonparametric identification of causal ef-
fects), Part II is about causal inference with models (i.e., estimation of causal
effects with parametric models), and Part III is about causal inference from
complex longitudinal data (i.e., estimation of causal effects of time-varying
treatments). Throughout the text, we have interspersed Fine Points and Tech-
nical points that elaborate on certain topics mentioned in the main text. Fine
Points are designed to be accessible to all readers while Technical Points are
designed for readers with intermediate training in statistics. The book provides
a cohesive presentation of concepts and methods for causal inference that are
currently scattered across journals in several disciplines. We expect that it
viii Causal Inference
will be of interest to all professionals that make causal inferences, including
epidemiologists, statisticians, psychologists, economists, sociologists, political
scientists, computer scientists. . .
This book grew out of our teaching and research activities. Several gener-
ations of inquisitive Harvard students helped us sharpen the contents of the
book. Decades of methodological work to quantify causal effects in health
applications helped us identify what matters in practice and distinguish the
essential from the incidental in our research. Therefore, this book needs to
be viewed as a (hopefully helpful) synthesis of our teaching and research ex-
perience rather than as a systematic review of all prior work. The book in-
cludes hundreds of citations—about a third to our own work—but we have, of
course, failed to reference every single important contribution to causal infer-
ence methodology. Also, because the field is vast and growing, no textbook can
stay totally up to date. We preemptively apologize to any colleagues who may
not see their work cited here and invite them to contact us. (Many did so dur-
ing the approximately two decades during which this book was available online
before its publication, and the book is better as a result.) Readers interested
in the history of a particular methodological development are encouraged to
read the academic papers that are referenced throughout the book.
We are grateful to many people who have made this book possible. Stephen
Cole, Issa Dahabreh, Sander Greenland, Jay Kaufman, Eleanor Murray, Thomas
Richardson, Sonja Swanson, Tyler VanderWeele, and Jan Vandenbroucke pro-
vided detailed comments. Goodarz Danaei, Kosuke Kawai, Martin Lajous,
and Kathleen Wirth helped create the NHEFS dataset. The sample code in
Part II was developed by Roger Logan in SAS, Eleanor Murray and Roger Lo-
gan in Stata, Joy Shi and Sean McGrath in R, and James Fiedler in Python.
Roger Logan has also been our LaTeX wizard. Randall Chaput helped create
the figures in Chapters 1 and 2. Josh McKible designed the book cover. Rob
Calver, our patient publisher, encouraged us to write the book and supported
our decision to make it freely available online.
In addition, multiple colleagues have helped us improve the book by de-
tecting typos and identifying unclear passages. We especially thank Kafui
Adjaye-Gbewonyo,
´
Alvaro Alonso, Katherine Almendinger, Ingelise Ander-
sen, Juan Jos´e Beunza, Karen Biala, Joanne Brady, Alex Breskin, Shan Cai,
Yu-Han Chiu, Alexis Dinno, John Ferguson, James Fiedler, Birgitte Fred-
eriksen, Tadayoshi Fushiki, Leticia Grize, Dominik Hangartner, Michael Hud-
gens, John Jackson, Marshall Joffe, Luke Keele, Laura Khan, Dae Hyun Kim,
Lauren Kunz, Mart´ın Lajous, Angeliki Lambrou, Wen Wei Loh, Haidong
Lu, Mohammad Ali Mansournia, Giovanni Marchetti, Lauren McCarl, Shira
Mitchell, Louis Mittel, Hannah Oh, Ibironke Olofin, Robert Paige, Jeremy
Pertman, Melinda Power, Bruce Psaty, Brian Sauer, Tomohiro Shinozaki, Ian
Shrier, Yan Song, Øystein Sørensen, Etsuji Suzuki, Denis Talbot, Mohammad
Tavakkoli, Sarah Taubman, Evan Thacker, Kun-Hsing Yu, Vera Zietemann,
Helmut Wasserbacher, Jessica Young, and Dorith Zimmermann.
Part I
Causal infe rence without models
Chapter 1
A DEFINITION OF CAUSAL EFFECT
As a human being, you are already familiar with causal inference’s fundamental concepts. Through sheer
existence, you know what a causal effect is, understand the difference between association and causation, and you
have used this knowledge consistently throughout your life. Had you not, you’d be dead. Without basic causal
concepts, you would not have survived long enough to read this chapter, let alone learn to read. As a toddler, you
would have jumped right into the swimming pool after seeing those who did were later able to reach the jam jar.
As a teenager, you would have skied down the most dangerous slopes after seeing those who did won the next ski
race. As a parent, you would have refused to give antibiotics to your sick child after observing that those children
who took their medicines were not at the park the next day.
Since you already understand the definition of causal effect and the difference between association and causation,
do not expect to gain deep conceptual insights from this chapter. Rather, the purpose of this chapter is to introduce
mathematical notation that formalizes the causal intuition that you already possess. Make sure that you can match
your causal intuition with the mathematical notation introduced here. This notation is necessary to precisely define
causal concepts, and will be used throughout the book.
1.1 Individual causal effects
Zeus is a patient waiting for a heart transplant. On January 1, he receives a
new heart. Five days later, he dies. Imagine that we can somehow know—
perhaps by divine revelation—that had Zeus not received a heart transplant
on January 1, he would have been alive five days later. Equipped with this
information most would agree that the transplant caused Zeus’s death. The
heart transplant intervention had a causal effect on Zeus’s five-day survival.
Another patient, Hera, also received a heart transplant on January 1. Five
days later she was alive. Imagine we can somehow know that, had Hera not
received the heart on January 1, she would still have been alive five days later.
Hence the transplant did not have a causal effect on Hera’s five-day survival.
These two vignettes illustrate how humans reason about causal effects: We
compare (usually only mentally) the outcome when an action A is taken versus
the outcome when the action A is withheld. If the two outcomes differ, we say
that the action A has a causal effect, causative or preventive, on the outcome.
Otherwise, we say that the action A has no causal effect on the outcome.
Epidemiologists, statisticians, economists, and other social scientists refer toKarma is another commonly used
term for actions that result in out-
comes.
the action A as an intervention, an exposure, a policy, or a treatment.
To make our causal intuition amenable to mathematical and statistical
analysis we will introduce some notation. Consider a dichotomous treatment
variable A (1: treated, 0: untreated) and a dichotomous outcome variable Y
(1: death, 0: survival). In this book we refer to variables such as A and YCapital letters represent random
variables. Lower case letters denote
particular values of a random vari-
able.
that may have different values for different individuals as random variables.
Let Y
a=1
(read Y under treatment a = 1) be the outcome variable that would
have been observed under the treatment value a = 1, and Y
a=0
(read Y under
treatment a = 0) the outcome variable that would have been observed under
4 A definition of causal effect
the treatment value a = 0. Y
a=1
and Y
a=0
are also random variables. Zeus
has Y
a=1
= 1 and Y
a=0
= 0 because he died when treated but would haveSometimes we abbreviate the ex-
pression “individual i has outcome
Y
a
= 1 ” by writing Y
a
i
= 1. Tech-
nically, when i refers to a specific
individual, such as Zeus, Y
a
i
is not
a random variable because we are
assuming that individual counter-
factual outcomes are deterministic
(see Technical Point 1.2).
survived if untreated, while Hera has Y
a=1
= 0 and Y
a=0
= 0 because she
survived when treated and would also have survived if untreated.
We can now provide a formal definition of a causal effect for an individ-
ual: The treatment A has a causal effect on an individual’s outcome Y if
Y
a=1
= Y
a=0
for the individual. Thus, the treatment has a causal effect on
Zeus’s outcome because Y
a=1
= 1 = 0 = Y
a=0
, but not on Hera’s outcome
because Y
a=1
= 0 = Y
a=0
. The variables Y
a=1
and Y
a=0
are referred to
as potential outcomes or as counterfactual outcomes. Some authors prefer the
Causal effect for individual i:
Y
a=1
i
= Y
a=0
i
term “potential outcomes” to emphasize that, depending on the treatment that
is received, either of these two outcomes can be potentially observed. Other
authors prefer the term “counterfactual outcomes” to emphasize that these
outcomes represent situations that may not actually occur (that is, counter-
to-the-fact situations).
For each individual, one of the counterfactual outcomes—the one that cor-
responds to the treatment value that the individual did receive—is actually
factual. For example, because Zeus was actually treated (A = 1), his counter-
factual outcome under treatment Y
a=1
= 1 is equal to his observed (actual)
outcome Y = 1. That is, an individual with observed treatment A equal to a,
has observed outcome Y equal to his counterfactual outcome Y
a
. This equality
can be succinctly expressed as Y = Y
A
where Y
A
denotes the counterfactual
Y
a
evaluated at the value a corresponding to the individual’s observed treat-
ment A. The equality Y = Y
A
is referred to as consistency.Consistency:
if A
i
= a, then Y
a
i
= Y
A
i
= Y
i
Individual causal effects are defined as a contrast of the values of counterfac-
tual outcomes, but only one of those outcomes is observed for each individual—
the one corresponding to the treatment value actually experienced by the in-
dividual. All other counterfactual outcomes remain unobserved. Because of
missing data, individual effects cannot be identified, i.e., they cannot be ex-
pressed as a function of the observed data (See Fine Point 2.1 for a possible
exception.)
1.2 Average causal effects
We needed three pieces of information to define an individual causal effect:
an outcome of interest, the actions a = 1 and a = 0 to be compared, and the
individual whose counterfactual outcomes Y
a=0
and Y
a=1
are to be compared.
However, because identifying individual causal effects is generally not possible,
we now turn our attention to an aggregated causal effect: the average causal
effect in a population of individuals. To define it, we need three pieces of
information: an outcome of interest, the actions a = 1 and a = 0 to be
compared, and a well-defined population of individuals whose outcomes Y
a=0
and Y
a=1
are to be compared.
Take Zeus’s extended family as our population of interest. Table 1.1 shows
the counterfactual outcomes under both treatment (a = 1) and no treatment
(a = 0) for all 20 members of our population. Focus on the last column: the
outcome Y
a=1
that would have been observed for each individual if they had
received the treatment (a heart transplant). Half of the members of the popu-
lation (10 out of 20) would have died if they had received a heart transplant.
That is, the proportion of individuals that would have developed the outcome
had all population individuals received a = 1 is Pr[Y
a=1
= 1] = 10/20 = 0.5.
1.2 Average causal effects 5
Fine Point 1.1
Interference. Our definition of a counterfactual outcome implicitly assumes that an individual’s counterfactual outcome
under treatment value a does not depend on other individuals’ treatment values. For example, we implicitly assumed
that Zeus would die if he received a heart transplant, regardless of whether Hera also received a heart transplant. That
is, Hera’s treatment value did not interfere with Zeus’s outcome. On the other hand, suppose that Hera’s getting
a new heart upsets Zeus to the extent that he would not survive his own heart transplant, even though he would
have survived had Hera not been transplanted. In this scenario, Hera’s treatment interferes with Zeus’s outcome.
Interference between individuals is common in studies that deal with contagious agents or educational programs, in
which an individual’s outcome is influenced by their social interaction with other population members.
In the presence of interference, the counterfactual Y
a
i
for an individual i is not well defined because an individual’s
outcome depends on other individuals’ treatment values. When there is interference, “the causal effect of heart transplant
on Zeus’s outcome” is not well defined. Rather, one needs to refer to “the causal effect of heart transplant on Zeus’s
outcome when Hera does not get a new heart” or “the causal effect of heart transplant on Zeus’s outcome when Hera
does get a new heart.” If other relatives and friends’ treatment also interfere with Zeus’s outcome, then one may need
to refer to the causal effect of heart transplant on Zeus’s outcome when “no relative or friend gets a new heart,” “when
only Hera gets a new heart,” etc. because the causal effect of treatment on Zeus’s outcome may differ for each particular
allocation of hearts. The assumption of no interference was labeled “no interaction between units” by Cox (1958), and
is included in the “stable-unit-treatment-value assumption (SUTVA)” described by Rubin (1980). See Halloran and
Struchiner (1995), Sobel (2006), Rosenbaum (2007), and Hudgens and Halloran (2009) for a more detailed discussion
of the role of interference in the definition of causal effects. Unless otherwise specified, we will assume no interference
throughout this book.
Similarly, from the other column of Table 1.1, we can conclude that half of
the members of the population (10 out of 20) would have died if they had notTable 1.1
Y
a=0
Y
a=1
Rheia 0 1
Kronos 1 0
Demeter 0 0
Hades 0 0
Hestia 0 0
Poseidon 1 0
Hera 0 0
Zeus 0 1
Artemis 1 1
Apollo 1 0
Leto 0 1
Ares 1 1
Athena 1 1
Hephaestus 0 1
Aphrodite 0 1
Polyphemus 0 1
Persephone 1 1
Hermes 1 0
Hebe 1 0
Dionysus 1 0
received a heart transplant. That is, the proportion of individuals that would
have developed the outcome had all population individuals received a = 0 is
Pr
Y
a=0
= 1
= 10/20 = 0.5. We have computed the counterfactual risk un-
der treatment to be 0.5 by counting the number of deaths (10) and dividing
them by the total number of individuals (20), which is the same as computing
the average of the counterfactual outcomes across all individuals in the pop-
ulation. To see the equivalence between risk and average for a dichotomous
outcome, use the data in Table 1.1 to compute the average of Y
a=1
.
We are now ready to provide a formal definition of the average causal
effect in the population: An average causal effect of treatment A on outcome
Y is present if Pr
Y
a=1
= 1
= Pr
Y
a=0
= 1
in the population of interest.
Under this definition, treatment A does not have an average causal effect on
outcome Y in our population because both the risk of death under treatment
Pr
Y
a=1
= 1
and the risk of death under no treatment Pr
Y
a=0
= 1
are
0.5. It does not matter whether all or none of the individuals receive a heart
transplant: Half of them would die in either case. When, like here, the average
causal effect in the population is null, we say that the null hypothesis of no
average causal effect is true. Because the risk equals the average and because
the letter E is usually employed to represent the population average or mean
(also referred to as ‘E’xpectation), we can rewrite the definition of a non-null
average causal effect in the population as E[Y
a=1
] = E[Y
a=0
] so that the
definition applies to both dichotomous and nondichotomous outcomes.
The presence of an “average causal effect of heart transplant A” is defined
by a contrast that involves the two actions “receiving a heart transplant (a =
1)” and “not receiving a heart transplant (a = 0).” When more than two
6 A definition of causal effect
Fine Point 1.2
Multiple versions of treatment. Our definition of a counterfactual outcome under treatment value a also implicitly
assumes that there is only one version of treatment value A = a. For example, we said that Zeus would die if he
received a heart transplant. This statement implicitly assumes that all heart transplants are performed by the same
surgeon using the same procedure and equipment. That is, there is only one version of the treatment “heart transplant.”
If there were multiple versions of treatment (e.g., surgeons with different skills), then it is possible that Zeus would
survive if his transplant were performed by Asclepios, and would die if his transplant were performed by Hygieia. In
the presence of multiple versions of treatment, the counterfactual Y
a
i
for an individual i is not well defined because an
individual’s outcome depends on the version of treatment a. When there are multiple versions of treatment, “the causal
effect of heart transplant on Zeus’s outcome” is not well defined. Rather, one needs to refer to “the causal effect of
heart transplant on Zeus’s outcome when Asclepios performs the surgery” or “the causal effect of heart transplant on
Zeus’s outcome when Hygieia performs the surgery.” If other components of treatment (e.g., procedure, place) are also
relevant to the outcome, then one may need to refer to “the causal effect of heart transplant on Zeus’s outcome when
Asclepios performs the surgery using his rod at the temple of Kos” because the causal effect of treatment on Zeus’s
outcome may differ for each particular version of treatment.
Like the assumption of no interference (see Fine Point 1.1), the assumption of no multiple versions of treatment
is included in the SUTVA described by Rubin (1980). Robins and Greenland (2000) made the point that if the
versions of a particular treatment (e.g., heart transplant) had the same causal effect on the outcome (survival), then the
counterfactual Y
a=1
would be well-defined. VanderWeele (2009a) formalized this point as the assumption of “treatment
variation irrelevance,” i.e., the assumption that multiple versions of treatment A = a may exist but they all result in
the same outcome Y
a
i
. We return to this issue in Chapter 3 but, unless otherwise specified, we will assume treatment
variation irrelevance throughout this book.
actions are possible (i.e., the treatment is not dichotomous), the particular
contrast of interest needs to be specified. For example, “the causal effect ofAverage causal effect in population:
E[Y
a=1
] = E[Y
a=0
] aspirin” is meaningless unless we specify that the contrast of interest is, say,
“taking, while alive, 150 mg of aspirin by mouth (or nasogastric tube if need be)
daily for 5 years” versus “not taking aspirin.” This causal effect is well defined
even if counterfactual outcomes under other interventions are not well defined
or do not exist (e.g., “taking, while alive, 500 mg of aspirin by absorption
through the skin daily for 5 years”).
Absence of an average causal effect does not imply absence of individual
effects. Table 1.1 shows that treatment has an individual causal effect on
12 members (including Zeus) of the population because, for each of these 12
individuals, the value of their counterfactual outcomes Y
a=1
and Y
a=0
differ.
Of the 12 , 6 were harmed by treatment, including Zeus
Y
a=1
− Y
a=0
= 1
,
and 6 were helped
Y
a=1
− Y
a=0
= −1
. This equality is not an accident:
The average causal effect E[Y
a=1
] − E[Y
a=0
] is always equal to the average
E[Y
a=1
− Y
a=0
] of the individual causal effects Y
a=1
− Y
a=0
, as a difference
of averages is equal to the average of the differences. When there is no causal
effect for any individual in the population, i.e., Y
a=1
= Y
a=0
for all individuals,
we say that the sharp causal null hypothesis is true. The sharp causal null
hypothesis implies the null hypothesis of no average effect.
As discussed in the next chapters, average causal effects can sometimes be
identified from data, even if individual causal effects cannot. Hereafter we refer
to ‘average causal effects’ simply as ‘causal effects’ and the null hypothesis of
no average effect as the causal null hypothesis. We next describe different
measures of the magnitude of a causal effect.
1.3 Measures of causal effect 7
Technical Point 1.1
Causal effects in the population. Let E[Y
a
] be the mean counterfactual outcome had all individuals in the population
received treatment level a. For discrete outcomes, the mean or expected value E[Y
a
] is defined as the weighted sum
P
y
y p
Y
a
(y) over all possible values y of the random variable Y
a
, where p
Y
a
(·) is the probability mass function of Y
a
,
i.e., p
Y
a
(y) = Pr [Y
a
= y]. For dichotomous outcomes, E[Y
a
] = Pr [Y
a
= 1]. For continuous outcomes, the expected
value E[Y
a
] is defined as the integral
R
yf
Y
a
(y) dy over all possible values y of the random variable Y
a
, where f
Y
a
(·)
is the probability density function of Y
a
. A common representation of the expected value that applies to both discrete
and continuous outcomes is E[Y
a
] =
R
y dF
Y
a
(y), where F
Y
a
(·) is the cumulative distribution function (cdf) of the
random variable Y
a
. We say that there is a non-null average causal effect in the population if E[Y
a
] = E[Y
a
′
] for any
two values a and a
′
.
The average causal effect, defined by a contrast of means of counterfactual outcomes, is the most commonly used
population causal effect. However, a population causal effect may also be defined as a contrast of functionals (including
the median, variance, hazard, or cdf) of counterfactual outcomes. In general, a population causal effect can be defined
as a contrast of any functional of the marginal distributions of counterfactual outcomes under different actions or
treatment values. For example the population causal effect on the variance is defined as V ar(Y
a=1
) − V ar(Y
a=0
),
which is zero for the population in Table 1.1 since the distribution of Y
a=1
and Y
a=0
are identical—both having 10
deaths out of 20. In fact, the equality of these distributions imply that for any functional (e.g., mean, variance, median,
hazard,etc.), the population causal effect on the functional is zero. However, in contrast to the mean, the difference in
population variances V ar(Y
a=1
) − V ar(Y
a=0
) does not in general equal the variance of the individual causal effects
V ar(Y
a=1
− Y
a=0
). For example, in Table 1.1, since Y
a=1
− Y
a=0
is not constant (−1 for 6 individuals, 1 for 6
individuals and 0 for 8 individuals), V ar(Y
a=1
− Y
a=0
) > 0 = V ar(Y
a=1
) − V ar(Y
a=0
). We will be able to identify
(i.e., compute) V ar(Y
a=1
) − V ar(Y
a=0
) from the data collected in a randomized trial, but not V ar(Y
a=1
− Y
a=0
)
because we can never simultaneously observe both Y
a=1
and Y
a=0
for any individual, and thus the covariance of Y
a=1
and Y
a=0
is not identified. The above discussion is true not only for the variance but for any nonlinear functional (e.g.,
median, hazard).
1.3 Measures of causal effect
We have seen that the treatment ‘heart transplant’ A does not have a causal
effect on the outcome ‘death’ Y in our population of 20 family members of
Zeus. The causal null hypothesis holds because the two counterfactual risks
Pr
Y
a=1
= 1
and Pr
Y
a=0
= 1
are equal to 0.5. There are equivalent ways
of representing the causal null. For example, we could say that the risk
Pr
Y
a=1
= 1
minus the risk Pr
Y
a=0
= 1
is zero (0.5 − 0.5 = 0) or that
the risk Pr
Y
a=1
= 1
divided by the risk Pr
Y
a=0
= 1
is one (0.5/0.5 = 1).
That is, we can represent the causal null byThe causal risk difference in the
population is the average of the in-
dividual causal effects Y
a=1
−Y
a=0
on the difference scale, i.e., it is
a measure of the average individ-
ual causal effect. By contrast, the
causal risk ratio in the population
is not the average of the individual
causal effects Y
a=1
/Y
a=0
on the
ratio scale, i.e., it is a measure of
causal effect in the population but
is not the average of any individual
causal effects.
(i) Pr
Y
a=1
= 1
− Pr
Y
a=0
= 1
= 0
(ii)
Pr
Y
a=1
= 1
Pr [Y
a=0
= 1]
= 1
(iii)
Pr
Y
a=1
= 1
/ Pr
Y
a=1
= 0
Pr [Y
a=0
= 1] / Pr [Y
a=0
= 0]
= 1
where the left-hand side of the equalities (i), (ii), and (iii) is the causal risk
difference, risk ratio, and odds ratio, respectively.
Suppose now that another treatment A, cigarette smoking, has a causal
effect on another outcome Y , lung cancer, in our population. The causal null
hypothesis does not hold: Pr
Y
a=1
= 1
and Pr
Y
a=0
= 1
are not equal. In
8 A definition of causal effect
Fine Point 1.3
Number needed to treat. Consider a population of 100 million patients in which 20 million would die within five years
if treated (a = 1), and 30 million would die within five years if untreated (a = 0). This information can be summarized
in several equivalent ways:
• the causal risk difference is Pr
Y
a=1
= 1
− Pr
Y
a=0
= 1
= 0.2 − 0.3 = −0.1
• if one treats the 100 million patients, there will be 10 million fewer deaths than if one does not treat those 100
million patients.
• one needs to treat 100 million patients to save 10 million lives
• on average, one needs to treat 10 patients to save 1 life
We refer to the average number of individuals that need to receive treatment a = 1 to reduce the number of cases
Y = 1 by one as the number needed to treat (NNT). In our example the NNT is equal to 10. For treatments that
reduce the average number of cases (i.e., the causal risk difference is negative), the NNT is equal to the reciprocal of
the absolute value of the causal risk difference:
NNT =
−1
Pr [Y
a=1
= 1] − Pr [Y
a=0
= 1]
For treatments that increase the average number of cases (i.e., the causal risk difference is positive), one can sym-
metrically define the number needed to harm. The NNT was introduced by Laupacis, Sackett, and Roberts (1988). Like
the causal risk difference, the NNT applies to the population and time interval on which it is based. For a discussion of
the relative advantages and disadvantages of the NNT as an effect measure, see Grieve (2003).
this setting, the causal risk difference, risk ratio, and odds ratio are not 0, 1,
and 1, respectively. Rather, these causal parameters quantify the strength of
the same causal effect on different scales. Because the causal risk difference,
risk ratio, and odds ratio (and other summaries) measure the causal effect, we
refer to them as effect measures.
Each effect measure may be used for different purposes. For example,
imagine a large population in which 3 in a million individuals would develop the
outcome if treated, and 1 in a million individuals would develop the outcome if
untreated. The causal risk ratio is 3, and the causal risk difference is 0.000002.
The causal risk ratio (multiplicative scale) is used to compute how many times
treatment, relative to no treatment, increases the disease risk. The causal risk
difference (additive scale) is used to compute the absolute number of cases of
the disease attributable to the treatment. The use of either the multiplicative
or additive scale will depend on the goal of the inference.
1.4 Random variability
At this point you could complain that our procedure to compute effect measures
is somewhat implausible. Not only did we ignore the well known fact that the
immortal Zeus cannot die, but—more to the point—our population in Table
1.1 had only 20 individuals. The populations of interest are typically much
larger.
1.4 Random variability 9
In our tiny population, we collected information from all the individuals. In
practice, investigators only collect information on a sample of the population
of interest. Even if the counterfactual outcomes of all study individuals were
known, working with samples prevents one from obtaining the exact proportion
of individuals in the population who had the outcome under treatment value
a, i.e., the probability of death under no treatment Pr
Y
a=0
= 1
cannot be
directly computed. One can only estimate this probability.
Consider the individuals in Table 1.1. We have previously viewed them as
forming a twenty-person population. Suppose we view them as a random sam-1
st
source of random error:
Sampling variability ple from a much larger, near-infinite super-population (e.g., all immortals). We
denote the proportion of individuals in the sample who would have died if unex-
posed as
c
Pr[Y
a=0
= 1] = 10/20 = 0.50. The sample proportion
c
Pr[Y
a=0
= 1]
does not have to be exactly equal to the proportion of individuals who would
have died if the entire super-population had been unexposed, Pr
Y
a=0
= 1
.
For example, suppose Pr
Y
a=0
= 1
= 0.57 in the population but, because
of random error due to sampling variability,
c
Pr
Y
a=0
= 1
= 0.5 in our par-
ticular sample. We use the sample proportion
c
Pr [Y
a
= 1] to estimate the
super-population probability Pr [Y
a
= 1] under treatment value a. The “hat”
over Pr indicates that the sample proportion
c
Pr [Y
a
= 1] is an estimator of
the corresponding population quantity Pr [Y
a
= 1]. We say that
c
Pr [Y
a
= 1]An estimator
ˆ
θ of θ is consistent
if, with probability approaching 1,
the difference
ˆ
θ−θ approaches zero
as the sample size increases towards
infinity.
is a consistent estimator of Pr [Y
a
= 1] because the larger the number of in-
dividuals in the sample, the smaller the difference between
c
Pr [Y
a
= 1] and
Pr [Y
a
= 1] is expected to be. This occurs because the error due to sampling
variability is random and thus obeys the law of large numbers.
Because the super-population probabilities Pr [Y
a
= 1] cannot be computed,
only consistently estimated by the sample proportions
c
Pr [Y
a
= 1], one cannotCaution: the term ‘consistency’
when applied to estimators has a
different meaning from that which
it has when applied to counterfac-
tual outcomes.
conclude with certainty that there is, or there is not, a causal effect. Rather, a
statistical procedure must be used to evaluate the empirical evidence regarding
the causal null hypothesis Pr
Y
a=1
= 1
= Pr
Y
a=0
= 1
(see Chapter 10 for
details).
So far we have only considered sampling variability as a source of random
error. But there may be another source of random variability: perhaps the
values of an individual’s counterfactual outcomes are not fixed in advance.2
nd
source of random error:
Nondeterministic counterfactuals We have defined the counterfactual outcome Y
a
as the individual’s outcome
had he received treatment value a. For example, in our first vignette, Zeus
would have died if treated and would have survived if untreated. As defined,
the values of the counterfactual outcomes are fixed or deterministic for each
individual, i.e., Y
a=1
= 1 and Y
a=0
= 0 for Zeus. In other words, Zeus has
a 100% chance of dying if treated and a 0% chance of dying if untreated.
However, we could imagine another scenario in which Zeus has a 90% chance
of dying if treated, and a 10% chance of dying if untreated. In this scenario,
the counterfactual outcomes are stochastic or nondeterministic because Zeus’s
probabilities of dying under treatment (0.9) and under no treatment (0.1)
are neither zero nor one. The values of Y
a=1
and Y
a=0
shown in Table 1.1
would be possible realizations of “random flips of mortality coins” with these
probabilities. Further, one would expect that these probabilities vary across
individuals because not all individuals are equally susceptible to develop the
outcome. Quantum mechanics, in contrast to classical mechanics, holds that
outcomes are inherently nondeterministic. That is, if the quantum mechanical
probability of Zeus dying is 90%, the theory holds that no matter how much
data we collect about Zeus, the uncertainty about whether Zeus will actually
develop the outcome if treated is irreducible.
10 A definition of causal effect
Technical Point 1.2
Nondeterministic counterfactuals. For nondeterministic counterfactual outcomes, the mean outcome under treatment
value a, E[Y
a
], equals the weighted sum
P
y
y p
Y
a
(y) over all possible values y of the random variable Y
a
, where the
probability mass function p
Y
a
(·) = E [Q
Y
a
(·)], and Q
Y
a
(y) is a random probability of having outcome Y = y under
treatment level a. In the example described in the text, Q
Y
a=1
(1) = 0.9 for Zeus. (For continuous outcomes, the
weighted sum is replaced by an integral.)
More generally, a nondeterministic definition of counterfactual outcome does not attach some particular value of
the random variable Y
a
to each individual, but rather an individual-specific statistical distribution Θ
Y
a
(·) of Y
a
.
The nondeterministic definition of causal effect is a generalization of the deterministic definition in which Θ
Y
a
(·) is
now a random cdf that may take values between 0 and 1. The average counterfactual outcome in the population
E[Y
a
] equals E {E [Y
a
| Θ
Y
a
(·)]}. Therefore, E[Y
a
] = E
R
y dΘ
Y
a
(y)
=
R
y d E[Θ
Y
a
(y)] =
R
y dF
Y
a
(y), where
F
Y
a
(·) = E
Θ
Y
a
i
(·)
.
If the counterfactual outcomes are binary and nondeterministic, the causal risk ratio in the population
E
[
Q
Y
a=1
(1)
]
E
[
Q
Y
a=0
(1)
]
is
equal to the weighted average E [W {Q
Y
a=1
(1) /Q
Y
a=0
(1)}] of the individual causal effects Q
Y
a=1
(1) /Q
Y
a=0
(1) on
the ratio scale, with weights W =
Q
Y
a=0
(1)
E
[
Q
Y
a=0
(1)
]
, provided Q
Y
a=0
(1) is never equal to 0 (i.e., deterministic) for anyone
in the population.
Thus, in causal inference, random error derives from sampling variability,
nondeterministic counterfactuals, or both. However, for pedagogic reasons, we
will continue to largely ignore random error until Chapter 10. Specifically, we
will assume that counterfactual outcomes are deterministic and that we have
recorded data on every individual in a very large (perhaps hypothetical) super-
population. This is equivalent to viewing our population of 20 individuals as a
population of 20 billion individuals in which 1 billion individuals are identical
to Zeus, 1 billion individuals are identical to Hera, and so on. Hence, until
Chapter 10, we will carry out our computations with Olympian certainty.
Then, in Chapter 10, we will describe how our statistical estimates and
confidence intervals for causal effects in the super-population are identical ir-
respective of whether the world is stochastic (quantum) or deterministic (classi-
cal) at the level of individuals. In contrast, confidence intervals for the average
causal effect in the actual study sample will differ depending on whether coun-
terfactuals are deterministic versus stochastic. Fortunately, super-population
effects are in most cases the causal effects of substantive interest.
1.5 Causation versus association
Obviously, the data available from actual studies look different from those
shown in Table 1.1. For example, we would not usually expect to learn Zeus’s
outcome if treated Y
a=1
and also Zeus’s outcome if untreated Y
a=0
. In the
real world, we only get to observe one of those outcomes because Zeus is either
treated or untreated. We referred to the observed outcome as Y . Thus, for
each individual, we know the observed treatment level A and the outcome Y
as in Table 1.2.
The data in Table 1.2 can be used to compute the proportion of individu-
als that developed the outcome Y among those individuals in the population
1.5 Causation versus association 11
that happened to receive treatment value a. For example, in Table 1.2, 7 in-
dividuals died (Y = 1) among the 13 individuals that were treated (A = 1).
Thus the risk of death in the treated, Pr [Y = 1|A = 1], was 7/13. More gener-
ally, the conditional probability Pr [Y = 1|A = a] is defined as the proportion
of individuals that developed the outcome Y among those individuals in the
population of interest that happened to receive treatment value a.
When the proportion of individuals who develop the outcome in the treated
Pr [Y = 1|A = 1] equals the proportion of individuals who develop the outcome
in the untreated Pr [Y = 1|A = 0], we say that treatment A and outcome Y
are independent, that A is not associated with Y , or that A does not predict
Y . Independence is represented by Y ⊥⊥A—or, equivalently, A⊥⊥Y — which isDawid (1979) introduced the sym-
bol ⊥⊥ to denote independence. read as Y and A are independent. Some equivalent definitions of independence
are
(i) Pr [Y = 1|A = 1] − Pr [Y = 1|A = 0] = 0
(ii)
Pr [Y = 1|A = 1]
Pr [Y = 1|A = 0]
= 1Table 1.2
A Y
Rheia 0 0
Kronos 0 1
Demeter 0 0
Hades 0 0
Hestia 1 0
Poseidon 1 0
Hera 1 0
Zeus 1 1
Artemis 0 1
Apollo 0 1
Leto 0 0
Ares 1 1
Athena 1 1
Hephaestus 1 1
Aphrodite 1 1
Polyphemus 1 1
Persephone 1 1
Hermes 1 0
Hebe 1 0
Dionysus 1 0
(iii)
Pr [Y = 1|A = 1] / Pr [Y = 0|A = 1]
Pr [Y = 1|A = 0] / Pr [Y = 0|A = 0]
= 1
where the left-hand side of the inequalities (i), (ii), and (iii) is the associational
risk difference, risk ratio, and odds ratio, respectively.
We say that treatment A and outcome Y are dependent or associated when
Pr [Y = 1|A = 1] = Pr [Y = 1|A = 0]. In our population, treatment and out-
For a continuous outcome Y we
define mean independence between
treatment and outcome as:
E[Y |A = 1] = E[Y |A = 0].
Independence and mean indepen-
dence are the same concept for di-
chotomous outcomes.
come are associated because Pr [Y = 1|A = 1] = 7/13 and Pr [Y = 1|A = 0] =
3/7. The associational risk difference, risk ratio, and odds ratio (and other
measures) quantify the strength of the association when it exists. They mea-
sure the association on different scales, and we refer to them as association
measures. These measures are also affected by random variability. However,
until Chapter 10, we will disregard statistical issues by assuming that the pop-
ulation in Table 1.2 is extremely large.
For dichotomous outcomes, the risk equals the average in the population,
and we can therefore rewrite the definition of association in the population as
E [Y |A = 1] = E [Y |A = 0]. For continuous outcomes Y , we will also define
association as E [Y |A = 1] = E [Y |A = 0]. For binary A, Y and A are not
associated if and only if they are not statistically correlated.
In our population of 20 individuals, we found (i) no causal effect after com-
paring the risk of death if all 20 individuals had been treated with the risk
of death if all 20 individuals had been untreated, and (ii) an association after
comparing the risk of death in the 13 individuals who happened to be treated
with the risk of death in the 7 individuals who happened to be untreated.
Figure 1.1 depicts the causation-association difference. The population (repre-
sented by a diamond) is divided into a white area (the treated) and a smaller
grey area (the untreated).
12 A definition of causal effect
Figure 1.1
The definition of causation implies a contrast between the whole white
diamond (all individuals treated) and the whole grey diamond (all individu-
als untreated), whereas association implies a contrast between the white (the
treated) and the grey (the untreated) areas of the original diamond. That is,
inferences about causation are concerned with what if questions in counterfac-
tual worlds, such as “what would be the risk if everybody had been treated?”
and “what would be the risk if everybody had been untreated?”, whereas infer-
ences about association are concerned with questions in the actual world, such
as “what is the risk in the treated?” and “what is the risk in the untreated?”
We can use the notation we have developed thus far to formalize this dis-
tinction between causation and association. The risk Pr [Y = 1|A = a] is a
conditional probability: the risk of Y in the subset of the population that
meet the condition ‘having actually received treatment value a’ (i.e., A = a).
In contrast the risk Pr [Y
a
= 1] is an unconditional—also known as marginal—
probability, the risk of Y
a
in the entire population. Therefore, association is
defined by a different risk in two disjoint subsets of the population determined
by the individuals’ actual treatment value (A = 1 or A = 0), whereas causa-
tion is defined by a different risk in the same population under two different
treatment values (a = 1 or a = 0). Throughout this book we often use theThe difference between association
and causation is critical. Suppose
the causal risk ratio of 5-year mor-
tality is 0.5 for aspirin vs. no as-
pirin, and the corresponding asso-
ciational risk ratio is 1.5 because
individuals at high risk of cardiovas-
cular death are preferentially pre-
scribed aspirin. After a physician
learns these results, she decides to
withhold aspirin from her patients
because those treated with aspirin
have a greater risk of dying com-
pared with the untreated. The doc-
tor will be sued for malpractice.
redundant expression ‘causal effect’ to avoid confusions with a common use of
‘effect’ meaning simply association.
These radically different definitions explain the well-known adage “asso-
ciation is not causation.” In our population, there was association because
the mortality risk in the treated (7/13) was greater than that in the untreated
(3/7). However, there was no causation because the risk if everybody had been
treated (10/20) was the same as the risk if everybody had been untreated. This
discrepancy between causation and association would not be surprising if those
who received heart transplants were, on average, sicker than those who did not
receive a transplant. In Chapter 7 we refer to this discrepancy as confounding.
Causal inference requires data like the hypothetical data in Table 1.1, but
all we can ever expect to have is real world data like those in Table 1.2. The
question is then under which conditions real world data can be used for causal
inference. The next chapter provides one answer: conduct a randomized ex-
periment.
Chapter 2
RANDOMIZED EXPERIMENTS
Does your looking up at the sky make other pedestrians look up too? This question has the main components
of any causal question: we want to know whether an action (your looking up) affects an outcome (other people’s
looking up) in a specific population (say, residents of Madrid in 2019). Suppose we challenge you to design a
scientific study to answer this question. “Not much of a challenge,” you say after some thought, “I can stand on
the sidewalk and flip a coin whenever someone approaches. If heads, I’ll look up; if tails, I’ll look straight ahead.
I’ll repeat the experiment a few thousand times. If the proportion of pedestrians who looked up within 10 seconds
after I did is greater than the proportion of pedestrians who looked up when I didn’t, I will conclude that my
looking up has a causal effect on other people’s looking up. By the way, I may hire an assistant to record what
people do while I’m looking up.” After conducting this study, you found that 55% of pedestrians looked up when
you looked up but only 1% looked up when you looked straight ahead.
Your solution to our challenge was to conduct a randomized experiment. It was an experiment because the
investigator (you) carried out the action of interest (looking up), and it was randomized because the decision to
act on any study subject (pedestrian) was made by a random device (coin flipping). Not all experiments are
randomized. For example, you could have looked up when a man approached and looked straight ahead when a
woman did. Then the assignment of the action would have followed a deterministic rule (up for man, straight for
woman) rather than a random mechanism. However, your findings would not have been nearly as convincing if
you had conducted a non randomized experiment. If your action had been determined by the pedestrian’s sex,
critics could argue that the “looking up” behavior of men and women differs (women may look up less often than
do men after you look up) and thus your study compared essentially “noncomparable” groups of people. This
chapter describes why randomization results in convincing causal inferences.
2.1 Randomization
In a real world study we will not know both of Zeus’s potential outcomes Y
a=1
under treatment and Y
a=0
under no treatment. Rather, we can only know
his observed outcome Y under the treatment value A that he happened to
receive. Table 2.1 summarizes the available information for our population
of 20 individuals. Only one of the two counterfactual outcomes is known for
each individual: the one corresponding to the treatment level that he actually
received. The data are missing for the other counterfactual outcomes. As weNeyman (1923) applied counterfac-
tual theory to the estimation of
causal effects via randomized ex-
periments.
discussed in the previous chapter, this missing data creates a problem because
it appears that we need the value of both counterfactual outcomes to compute
effect measures. The data in Table 2.1 are only good to compute association
measures.
Randomized experiments, like any other real world study, generate data
with missing values of the counterfactual outcomes as shown in Table 2.1.
However, randomization ensures that those missing values occurred by chance.
As a result, effect measures can be computed —or, more rigorously, consistently
estimated—in randomized experiments despite the missing data. Let us be
more precise.
Suppose that the population represented by a diamond in Figure 1.1 was
14 Randomized experiments
near-infinite, and that we flipped a coin for each individual in such population.
We assigned the individual to the white group if the coin turned tails, and
to the grey group if it turned heads. Note this was not a fair coin becauseTable 2.1
A Y Y
0
Y
1
Rheia 0 0 0 ?
Kronos 0 1 1 ?
Demeter 0 0 0 ?
Hades 0 0 0 ?
Hestia 1 0 ? 0
Poseidon 1 0 ? 0
Hera 1 0 ? 0
Zeus 1 1 ? 1
Artemis 0 1 1 ?
Apollo 0 1 1 ?
Leto 0 0 0 ?
Ares 1 1 ? 1
Athena 1 1 ? 1
Hephaestus 1 1 ? 1
Aphrodite 1 1 ? 1
Polyphemus 1 1 ? 1
Persephone 1 1 ? 1
Hermes 1 0 ? 0
Hebe 1 0 ? 0
Dionysus 1 0 ? 0
the probability of heads was less than 50%—fewer people ended up in the
grey group than in the white group. Next we asked our research assistants to
administer the treatment of interest (A = 1), to individuals in the white group
and a placebo (A = 0) to those in the grey group. Five days later, at the end of
the study, we computed the mortality risks in each group, Pr [Y = 1|A = 1] =
0.3 and Pr [Y = 1|A = 0] = 0.6. The associational risk ratio was 0.3/0.6 = 0.5
and the associational risk difference was 0.3 − 0.6 = −0.3. We will assume
that this was an ideal randomized experiment in all other respects: no loss to
follow-up, full adherence to the assigned treatment over the duration of the
study, a single version of treatment, and double blind assignment (see Chapter
9). Ideal randomized experiments are unrealistic but useful to introduce some
key concepts for causal inference. Later in this book we consider more realistic
randomized experiments.
Now imagine what would have happened if the research assistants had
misinterpreted our instructions and had treated the grey group rather than
the white group. Say we learned of the misunderstanding after the study
finished. How does this reversal of treatment status affect our conclusions?
Not at all. We would still find that the risk in the treated (now the grey
group) Pr [Y = 1|A = 1] is 0.3 and the risk in the untreated (now the white
group) Pr [Y = 1|A = 0] is 0.6. The association measure would not change.
Because individuals were randomly assigned to white and grey groups, the
proportion of deaths among the exposed, Pr [Y = 1|A = 1] is expected to be
the same whether individuals in the white group received the treatment and
individuals in the grey group received placebo, or vice versa. When group
membership is randomized, which particular group received the treatment is
irrelevant for the value of Pr [Y = 1|A = 1]. The same reasoning applies to
Pr [Y = 1|A = 0], of course. Formally, we say that groups are exchangeable.
Exchangeability means that the risk of death in the white group would have
been the same as the risk of death in the grey group had individuals in the white
group received the treatment given to those in the grey group. That is, the risk
under the potential treatment value a among the treated, Pr [Y
a
= 1|A = 1],
equals the risk under the potential treatment value a among the untreated,
Pr [Y
a
= 1|A = 0], for both a = 0 and a = 1. An obvious consequence of these
(conditional) risks being equal in all subsets defined by treatment status in the
population is that they must be equal to the (marginal) risk under treatment
value a in the whole population: Pr [Y
a
= 1|A = 1] = Pr [Y
a
= 1|A = 0] =
Pr [Y
a
= 1]. Because the counterfactual risk under treatment value a is the
same in both groups A = 1 and A = 0, we say that the actual treatment A
does not predict the counterfactual outcome Y
a
. Equivalently, exchangeability
means that the counterfactual outcome and the actual treatment are indepen-
dent, or Y
a
⊥⊥A, for all values a. Randomization is so highly valued because itExchangeability:
Y
a
⊥⊥A for all a. See also Techni-
cal Point 2.1 for other versions of
exchangeability.
is expected to produce exchangeability. When the treated and the untreated
are exchangeable, we sometimes say that treatment is exogenous, and thus
exogeneity is commonly used as a synonym for exchangeability.
The previous paragraph argues that, in the presence of exchangeability, the
counterfactual risk under treatment in the white part of the population would
equal the counterfactual risk under treatment in the entire population. But the
risk under treatment in the white group is not counterfactual at all because the
white group was actually treated! Therefore our ideal randomized experiment
allows us to compute the counterfactual risk under treatment in the population
2.1 Randomization 15
Technical Point 2.1
Full exchangeability and mean exchangeability. Randomization makes the Y
a
jointly independent of A which implies,
but is not implied by, exchangeability Y
a
⊥⊥A for each a. Formally, let A = {a, a
′
, a
′′
, ...} denote the set of all treatment
values present in the population, and Y
A
=
n
Y
a
, Y
a
′
, Y
a
′′
, ...
o
the set of all counterfactual outcomes. Randomization
makes Y
A
⊥⊥A. We refer to this joint independence as full exchangeability. For a dichotomous treatment, A = {0, 1}
and full exchangeability is
Y
a=1
, Y
a=0
⊥⊥A.
For a dichotomous outcome and treatment, exchangeability Y
a
⊥⊥A can also be written as Pr [Y
a
= 1|A = 1] =
Pr [Y
a
= 1|A = 0] or, equivalently, as E[Y
a
|A = 1] = E[Y
a
|A = 0] for all a. We refer to the last equality as mean
exchangeability. For a continuous outcome, exchangeability Y
a
⊥⊥A implies mean exchangeability E[Y
a
|A = a
′
] =
E[Y
a
], but mean exchangeability does not imply exchangeability because distributional parameters other than the mean
(e.g., variance) may not be independent of treatment.
Neither full exchangeability Y
A
⊥⊥A nor exchangeability Y
a
⊥⊥A are required to prove that E[Y
a
] = E[Y |A = a].
Mean exchangeability is sufficient. As sketched in the main text, the proof has two steps. First, E[Y |A = a] =
E[Y
a
|A = a] by consistency. Second, E[Y
a
|A = a] = E[Y
a
] by mean exchangeability. Because exchangeability and
mean exchangeability are identical concepts for the dichotomous outcomes used in this chapter, we use the shorter term
“exchangeability” throughout.
Pr
Y
a=1
= 1
because it is equal to the risk in the treated Pr [Y = 1|A = 1] =
0.3. That is, the risk in the treated (the white part of the diamond) is the
same as the risk if everybody had been treated (and thus the diamond had
been entirely white). Of course, the same rationale applies to the untreated:
the counterfactual risk under no treatment in the population Pr
Y
a=0
= 1
equals the risk in the untreated Pr [Y = 1|A = 0] = 0.6. The causal risk ratio
is 0.5 and the causal risk difference is −0.3. In ideal randomized experiments,
association is causation.
Here is another explanation for exchangeability Y
a
⊥⊥A in a randomized
experiment. The counterfactual outcome Y
a
, like one’s genetic make-up, can
be thought of as a fixed characteristic of a person existing before the treat-
ment A was randomly assigned. This is because Y
a
encodes what would have
been one’s outcome if assigned to treament a and thus does not depend on
the treatment you later receive. Because treatment A was randomized, it is
independent of both your genes and Y
a
. The difference between Y
a
and your
genetic make-up is that, even conceptually, you can only learn the value of Y
a
after treatment is given and then only if one’s treatment A is equal to a.
Before proceeding, please make sure you understand the difference betweenCaution:
Y
a
⊥⊥ A is different from Y ⊥⊥A. Y
a
⊥⊥A and Y ⊥⊥A. Exchangeability Y
a
⊥⊥A is defined as independence between
the counterfactual outcome and the observed treatment. Again, this means
that the treated and the untreated would have experienced the same risk of
death if they had received the same treatment level (either a = 0 or a = 1). But
independence between the counterfactual outcome and the observed treatment
Y
a
⊥⊥A does not imply independence between the observed outcome and the
observed treatment Y ⊥⊥A. For example, in a randomized experiment in which
exchangeability Y
a
⊥⊥A holds and the treatment has a causal effect on theSuppose there is a causal effect on
some individuals so that Y
a=1
=
Y
a=0
. Since Y = Y
A
, then Y
a
with a evaluated at the observed
treatment A is the observed Y
A
,
which depends on A, and thus will
not be independent of A.
outcome, then Y ⊥⊥A does not hold because the treatment is associated with
the observed outcome.
Does exchangeability hold in our heart transplant study of Table 2.1? To
answer this question we would need to check whether Y
a
⊥⊥A holds for a = 0
and for a = 1. Take a = 0 first. Suppose the counterfactual data in Table 1.1
are available to us. We can then compute the risk of death under no treatment
16 Randomized experiments
Fine Point 2.1
Crossover experiments. Suppose we want to estimate the individual causal effect of lightning bolt use A on Zeus’s
blood pressure Y . We define the counterfactual outcomes Y
a=1
and Y
a=0
to be 1 if Zeus’s blood pressure is temporarily
elevated after calling or not calling a lightning strike, respectively. Suppose we convinced Zeus to use his lightning bolt
only when suggested by us. Yesterday morning we asked Zeus to call a lightning strike (a = 1). His blood pressure was
elevated after doing so. This morning we asked Zeus to refrain from using his lightning bolt (a = 0). His blood pressure
did not increase. We have conducted a crossover experiment in which an individual’s outcome is sequentially observed
under two treatment values. One might argue that, because we have observed both of Zeus’s counterfactual outcomes
Y
a=1
= 1 and Y
a=0
= 0, using a lightning bolt has a causal effect on Zeus’s blood pressure. However, this argument
is generally incorrect unless the very strong assumptions i)–iii) given in the next paragraph are true.
In crossover experiments, individuals are observed during two or more periods, say t = 0 and t = 1. An individual i
receives a different treatment value A
it
in each period t. Let Y
a
0
a
1
i1
be the (deterministic) counterfactual outcome at
t = 1 for individual i if treated with a
1
at t = 1 and a
0
at t = 0. Let Y
a
0
i0
be defined similarly for t = 0. The individual
causal effect Y
a
t
=1
it
−Y
a
t
=0
it
can be identified if the following three conditions hold: i) no carryover effect of treatment:
Y
a
0
,a
1
it=1
= Y
a
1
it=1
, ii) the individual causal effect does not depend on time: Y
a
t
=1
it
− Y
a
t
=0
it
= α
i
for t = 0, 1, and iii) the
counterfactual outcome under no treatment does not depend on time: Y
a
t
=0
it
= β
i
for t = 0, 1. Under these conditions,
if the individual is treated at time 1 (A
i1
= 1) but not time 0 (A
i0
= 0) then, by consistency, Y
i1
−Y
i0
is the individual
causal effect because Y
i1
−Y
i0
= Y
a
1
=1
i1
−Y
a
0
=0
i0
= Y
a
1
=1
i1
−Y
a
1
=0
i1
+ Y
a
1
=0
i1
−Y
a
0
=0
i0
= α
i
+ β
i
−β
i
= α
i
. Similarly
if A
i1
= 0 and A
i0
= 1, Y
i0
− Y
i1
= α
i
is the individual level causal effect.
Condition (i) implies that the outcome Y
a
t
it
has an abrupt onset that completely resolves by the next time period.
Hence, crossover experiments cannot be used to study the effect of heart transplant, an irreversible action, on death,
an irreversible outcome. See also Fine Point 3.2.
Pr
Y
a=0
= 1|A = 1
= 7/13 in the 13 treated individuals and the risk of death
under no treatment Pr
Y
a=0
= 1|A = 0
= 3/7 in the 7 untreated individuals.
Since the risk of death under no treatment is greater in the treated than in
the untreated individuals, i.e., 7/13 > 3/7, we conclude that the treated have
a worse prognosis than the untreated, i.e., that the treated and the untreated
are not exchangeable. Mathematically, we have proven that exchangeability
Y
a
⊥⊥A does not hold for a = 0. (You can check that it does not hold for a = 1
either.) Thus the answer to the question that opened this paragraph is ‘No’.Reminder: Our discussion of ran-
domized experiments refers to pop-
ulation or average causal effects be-
cause individual causal effects can-
not generally be identified. See
Fine Point 2.1.
But only the observed data in Table 2.1, not the counterfactual data in
Table 1.1, are available in the real world. Since Table 2.1 is insufficient to
compute counterfactual risks like the risk under no treatment in the treated
Pr
Y
a=0
= 1|A = 1
, we are generally unable to determine whether exchange-
ability holds in our study. However, suppose for a moment, that we actually
had access to Table 1.1 and determined that exchangeability does not hold
in our heart transplant study. Can we then conclude that our study is not
a randomized experiment? No, for two reasons. First, as you are probably
already thinking, a twenty-person study is too small to reach definite conclu-
sions. Random fluctuations arising from sampling variability could explain
almost anything. We will discuss random variability in Chapter 10. Until
then, let us assume that each individual in our population represents 1 billion
individuals that are identical to him or her. Second, it is still possible that
a study is a randomized experiment even if exchangeability does not hold in
infinite samples. However, unlike the type of randomized experiment described
in this section, it would need to be a randomized experiment in which investi-
gators use more than one coin to randomly assign treatment. The next section
describes randomized experiments with more than one coin.
2.2 Conditional randomization 17
2.2 Conditional randomization
Table 2.2 shows the data from our heart transplant randomized study. Besides
data on treatment A (1 if the individual received a transplant, 0 otherwise)Table 2.2
L A Y
Rheia 0 0 0
Kronos 0 0 1
Demeter 0 0 0
Hades 0 0 0
Hestia 0 1 0
Poseidon 0 1 0
Hera 0 1 0
Zeus 0 1 1
Artemis 1 0 1
Apollo 1 0 1
Leto 1 0 0
Ares 1 1 1
Athena 1 1 1
Hephaestus 1 1 1
Aphrodite 1 1 1
Polyphemus 1 1 1
Persephone 1 1 1
Hermes 1 1 0
Hebe 1 1 0
Dionysus 1 1 0
and outcome Y (1 if the individual died, 0 otherwise), Table 2.2 also contains
data on the prognostic factor L (1 if the individual was in critical condition,
0 otherwise), which we measured before treatment was assigned. We now
consider two mutually exclusive study designs and discuss whether the data in
Table 2.2 could have arisen from either of them.
In design 1 we would have randomly selected 65% of the individuals in the
population and transplanted a new heart to each of the selected individuals.
That would explain why 13 out of 20 individuals were treated. In design 2
we would have classified all individuals as being in either critical (L = 1)
or noncritical (L = 0) condition. Then we would have randomly selected
75% of the individuals in critical condition and 50% of those in noncritical
condition, and transplanted a new heart to each of the selected individuals.
That would explain why 9 out of 12 individuals in critical condition, and 4 out
of 8 individuals in non critical condition, were treated.
Both designs are randomized experiments. Design 1 is precisely the type of
randomized experiment described in Section 2.1. Under this design, we would
use a single coin to assign treatment to all individuals (e.g., treated if tails,
untreated if heads): a loaded coin with probability 0.65 of turning tails, thus
resulting in 65% of the individuals receiving treatment. Under design 2 we
would not use a single coin for all individuals. Rather, we would use a coin
with a 0.75 chance of turning tails for individuals in critical condition, and
another coin with a 0.50 chance of turning tails for individuals in non critical
condition. We refer to design 2 experiments as conditionally randomized ex-
periments because we use several randomization probabilities that depend (are
conditional) on the values of the variable L. We refer to design 1 experiments
as marginally randomized experiments because we use a single unconditional
(marginal) randomization probability that is common to all individuals.
As discussed in the previous section, a marginally randomized experiment
is expected to result in exchangeability of the treated and the untreated:
Pr [Y
a
= 1|A = 1] = Pr [Y
a
= 1|A = 0] or Y
a
⊥⊥A for all a.
In contrast, a conditionally randomized experiment will not generally result
in exchangeability of the treated and the untreated because, by design, each
group may have a different proportion of individuals with bad prognosis.
Thus the data in Table 2.2 could not have arisen from a marginally random-
ized experiment because 69% treated versus 43% untreated individuals were
in critical condition. This imbalance indicates that the risk of death in the
treated, had they remained untreated, would have been higher than the risk
of death in the untreated. That is, treatment A predicts the counterfactual
risk of death under no treatment, and exchangeability Y
a
⊥⊥A does not hold.
Since our study was a randomized experiment, you can safely conclude that
the study was a randomized experiment with randomization conditional on L.
Our conditionally randomized experiment is simply the combination of two
separate marginally randomized experiments: one conducted in the subset of
individuals in critical condition (L = 1), the other in the subset of individuals
in non critical condition (L = 0). Consider first the randomized experiment
being conducted in the subset of individuals in critical condition. In this subset,
the treated and the untreated are exchangeable. Formally, the counterfactual
mortality risk under each treatment value a is the same among the treated
18 Randomized experiments
and the untreated given that they all were in critical condition at the time of
treatment assignment. That is,
Pr [Y
a
= 1|A = 1, L = 1] = Pr [Y
a
= 1|A = 0, L = 1] or Y
a
⊥⊥A|L = 1 for all a,
where Y
a
⊥⊥A|L = 1 means Y
a
and A are independent given L = 1. Simi-
larly, randomization also ensures that the treated and the untreated are ex-
changeable in the subset of individuals that were in noncritical condition, i.e.,
Y
a
⊥⊥A|L = 0. When Y
a
⊥⊥A|L = l holds for all values l we simply write
Y
a
⊥⊥A|L. Thus, although conditional randomization does not guarantee un-Conditional exchangeability:
Y
a
⊥⊥A|L for all a conditional (or marginal) exchangeability Y
a
⊥⊥A, it guarantees conditional
exchangeability Y
a
⊥⊥A|L within levels of the variable L. In summary, ran-
domization produces either marginal exchangeability (design 1) or conditional
exchangeability (design 2).
We know how to compute effect measures under marginal exchangeabil-
ity: the causal risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
equals the associa-
tional risk ratio Pr [Y = 1|A = 1] / Pr [Y = 1|A = 0] in marginally randomized
experiments because exchangeability ensures that the counterfactual risk un-If A = 1, Y
a=0
is missing;
if A = 0, Y
a=1
is miss-
ing. Data are missing com-
pletely at random (MCAR)
if Pr
A = a|L, Y
a=1
, Y
a=0
=
Pr [A = a], which holds in a
marginally randomized exper-
iment. Data are missing at
random (MAR) if the probability
of A = a conditional on the full
data (L, Y
a=1
, Y
a=0
) only depends
on the data that would be observed
(L, Y
a
) if A = a. In fact, MAR im-
plies Pr
A = a|L, Y
a=1
, Y
a=0
=
Pr [A = a|L], which holds in
a conditionally randomized ex-
periment because, by MAR,
Pr
A = 1|L, Y
a=1
, Y
a=0
cannot depend on Y
a=0
and
1 − Pr
A = 1|L, Y
a=1
, Y
a=0
=
Pr
A = 0|L, Y
a=1
, Y
a=0
cannot
depend on Y
a=1
. The terms
MCAR, MAR, and MNAR (missing
not at random) were introduced by
Rubin (1976).
der treatment level a, Pr [Y
a
= 1], equals the observed risk among those who
received treatment level a, Pr [Y = 1|A = a]. Thus, if the data in Table 2.2 had
been collected during a marginally randomized experiment, the causal risk ra-
tio would be readily calculated from the data on A and Y as
7/13
3/7
= 1.26. The
question is how to compute the causal risk ratio in a conditionally randomized
experiment. Remember that a conditionally randomized experiment is simply
the combination of two (or more) separate marginally randomized experiments
conducted in different subsets of the population L = 1 and L = 0. Thus we
have two options.
First, we compute the average causal effect in each of these subsets or strata
of the population. Because association is causation within each subset, the
stratum-specific causal risk ratio Pr
Y
a=1
= 1|L = 1
/ Pr
Y
a=0
= 1|L = 1
among people in critical condition is equal to the stratum-specific associational
risk ratio Pr [Y = 1|L = 1, A = 1] / Pr [Y = 1|L = 1, A = 0] among people in
critical condition. And analogously for L = 0. We refer to this method to com-
pute stratum-specific causal effects as stratification. Note that the stratum-
specific causal risk ratio in the subset L = 1 may differ from the causal risk
ratio in L = 0. In that case, we say that the effect of treatment is modified
by L, or that there is effect modification by L or that there is treatment ef-
fect heterogeneity across levels of L. Stratification and effect modification are
discussed in more detail in Chapter 4.
Second, we compute the average causal effect Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
in the entire population, as we have been doing so far. Whether our principal
interest lies in the stratum-specific average causal effects versus the average
causal effect in the entire population depends on practical and theoretical con-
siderations discussed in detail in Chapter 4 and in Part III. As one example,
you may be interested in the average causal effect in the entire population,
rather than in the stratum-specific average causal effects, if you do not expect
to have information on L for future individuals (e.g., the variable L is expen-
sive to measure) and thus your decision to treat cannot depend on the value of
L. Until Chapter 4, we will restrict our attention to the average causal effect
in the entire population. The next two sections describe how to use data from
conditionally randomized experiments to compute the average causal effect in
the entire population. See also Fine Point 2.2 for a discussion of risk periods.
2.3 Standardization 19
Fine Point 2.2
Risk periods. We have defined a risk as the proportion of individuals who develop the outcome of interest during a
particular period. For example, the 5-day mortality risk in the treated Pr [Y = 1|A = 1] is the proportion of treated
individuals who died during the first five days of follow-up. Throughout the book we often specify the period when the
risk is first defined (e.g., 5 days) and, for conciseness, omit it later. That is, we may just say “the mortality risk” rather
than “the five-day mortality risk.”
The following example highlights the importance of specifying the risk period. Suppose a randomized experiment was
conducted to quantify the causal effect of antibiotic therapy on mortality among elderly humans infected with the plague
bacteria. An investigator analyzes the data and concludes that the causal risk ratio is 0.05, i.e., on average antibiotics
decrease mortality by 95%. A second investigator also analyzes the data but concludes that the causal risk ratio is
1, i.e., antibiotics have a null average causal effect on mortality. Both investigators are correct. The first investigator
computed the ratio of 1-year risks, whereas the second investigator computed the ratio of 100-year risks. The 100-year
risk was of course 1 regardless of whether individuals received the treatment. When we say that a treatment has a
causal effect on mortality, we mean that death is delayed, not prevented, by the treatment.
2.3 Standardization
Our heart transplant study is a conditionally randomized experiment: the in-
vestigators used a random procedure to assign hearts (A = 1) with probability
50% to the 8 individuals in noncritical condition (L = 0), and with probability
75% to the 12 individuals in critical condition (L = 1). First, let us focus
on the 8 individuals—remember, they are really the average representatives
of 8 billion individuals—in noncritical condition. In this group, the risk of
death among the treated is Pr [Y = 1|L = 0, A = 1] =
1
4
, and the risk of death
among the untreated is Pr [Y = 1|L = 0, A = 0] =
1
4
. Because treatment was
randomly assigned to individuals in the group L = 0, i.e., Y
a
⊥⊥A|L = 0, the
observed risks are equal to the counterfactual risks. That is, in the group
L = 0, the risk in the treated equals the risk if everybody had been treated,
Pr [Y = 1|L = 0, A = 1] = Pr
Y
a=1
= 1|L = 0
, and the risk in the untreated
equals the risk if everybody had been untreated, Pr [Y = 1|L = 0, A = 0] =
Pr
Y
a=0
= 1|L = 0
. Following a similar reasoning, we can conclude that the
observed risks equal the counterfactual risks in the group of 12 individuals
in critical condition, i.e., Pr [Y = 1|L = 1, A = 1] = Pr
Y
a=1
= 1|L = 1
=
2
3
,
and Pr [Y = 1|L = 1, A = 0] = Pr
Y
a=0
= 1|L = 1
=
2
3
.
Suppose now that our goal is to compute the causal risk ratio Pr[Y
a=1
=
1]/ Pr[Y
a=0
= 1]. The numerator of the causal risk ratio is the risk if all 20
individuals in the population had been treated. From the previous paragraph,
we know that the risk if all individuals had been treated is
1
4
in the 8 individuals
with L = 0 and
2
3
in the 12 individuals with L = 1. Therefore the risk if all 20
individuals in the population had been treated will be a weighted average of
1
4
and
2
3
in which each group receives a weight proportional to its size. Since
40% of the individuals (8) are in group L = 0 and 60% of the individuals (12)
are in group L = 1, the weighted average is
1
4
× 0.4 +
2
3
× 0.6 = 0.5. Thus the
risk if everybody had been treated Pr[Y
a=1
= 1] is equal to 0.5. By following
the same reasoning we can calculate that the risk if nobody had been treated
Pr[Y
a=0
= 1] is also equal to 0.5. The causal risk ratio is then 0.5/0.5 = 1.
More formally, the marginal counterfactual risk Pr[Y
a
= 1] is the weighted
average of the stratum-specific risks Pr[Y
a
= 1|L = 0] and Pr[Y
a
= 1|L = 1]
with weights equal to the proportion of individuals in the population with
20 Randomized experiments
L = 0 and L = 1, respectively. That is, Pr[Y
a
= 1] = Pr[Y
a
= 1|L =
0] Pr [L = 0] + Pr[Y
a
= 1|L = 1] Pr [L = 1]. Or, using a more compact
notation, Pr[Y
a
= 1] =
P
l
Pr[Y
a
= 1|L = l] Pr [L = l], where
P
l
means
sum over all values l that occur in the population. Under conditional ex-
changeability, we can replace the counterfactual risk Pr[Y
a
= 1|L = l] by
the observed risk Pr[Y = 1|L = l, A = a] in the expression above. That is,
Pr[Y
a
= 1] =
P
l
Pr[Y = 1|L = l, A = a] Pr [L = l]. The left-hand side of
this equality is an unobserved counterfactual risk whereas the right-hand side
includes observed quantities only, which can be computed using data on L,
A, and Y . When, as here, a counterfactual quantity can be expressed as a
function of the distribution (i.e., the probabilities) of the observed data, we
say that the counterfactual quantity is identified (or identifiable); otherwise,
we say it is unidentified.
This method is known in epidemiology, demography, and other disciplines
as standardization. For example, the numerator
P
l
Pr[Y = 1|L = l, A =Standardized mean
P
l
E[Y |L = l, A = a]
×Pr [L = l]
1] Pr [L = l] of the causal risk ratio is the standardized risk in the treated
using the population as the standard. Under conditional exchangeability, this
standardized risk can be interpreted as the (counterfactual) risk that would
have been observed had all the individuals in the population been treated.
The standardized risks in the treated and the untreated are equal to the
counterfactual risks under treatment and no treatment, respectively. There-
fore, the causal risk ratio
Pr[Y
a=1
= 1]
Pr[Y
a=0
= 1]
can be computed by standardization as
P
l
Pr[Y = 1|L = l, A = 1] Pr [L = l]
P
l
Pr[Y = 1|L = l, A = 0] Pr [L = l]
.
2.4 Inverse probability weighting
In the previous section we computed the causal risk ratio in a conditionally
randomized experiment via standardization. In this section we compute this
causal risk ratio via inverse probability weighting. The data in Table 2.2
can be displayed as a tree in which all 20 individuals start at the left and
progress over time towards the right, as in Figure 2.1. The leftmost circle of
the tree contains its first branching: 8 individuals were in non critical condi-
tion (L = 0) and 12 in critical condition (L = 1). The numbers in parenthesesFigure 2.1 is an example of a
fully randomized causally inter-
preted structured tree graph or FR-
CISTG (Robins 1986, 1987) rep-
resentation of a conditionally ran-
domized experiment. Did we win
the prize for the worst acronym
ever?
are the probabilities of being in noncritical, Pr [L = 0] = 8/20 = 0.4, or crit-
ical, Pr [L = 1] = 12/20 = 0.6, condition. Let us follow, e.g., the branch
L = 0. Of the 8 individuals in this branch, 4 were untreated (A = 0) and
4 were treated (A = 1). The conditional probability of being untreated is
Pr [A = 0|L = 0] = 4/8 = 0.5, as shown in parentheses. The conditional prob-
ability of being treated Pr [A = 1|L = 0] is 0.5 too. The upper right circle
represents that, of the 4 individuals in the branch (L = 0, A = 0), 3 survived
(Y = 0) and 1 died (Y = 1). That is, Pr [Y = 0|L = 0, A = 0] = 3/4 and
Pr [Y = 1|L = 0, A = 0] = 1/4. The other branches of the tree are interpreted
analogously. The circles contain the bifurcations defined by non treatment
variables. We now use this tree to compute the causal risk ratio.
2.4 Inverse probability weighting 21
Figure 2.1
Figure 2.2
The denominator of the causal risk ratio, Pr[Y
a=0
= 1], is the counterfactual
risk of death had everybody in the population remained untreated. Let us
calculate this risk. In Figure 2.1, 4 out of 8 individuals with L = 0 were
untreated, and 1 of them died. How many deaths would have occurred had
the 8 individuals with L = 0 remained untreated? Two deaths, because if 8
individuals rather than 4 individuals had remained untreated, then 2 deaths
rather than 1 death would have been observed. If the number of individuals is
multiplied times 2, then the number of deaths is also doubled. In Figure 2.1,
3 out of 12 individuals with L = 1 were untreated, and 2 of them died. How
many deaths would have occurred had the 12 individuals with L = 1 remained
untreated? Eight deaths, or 2 deaths times 4, because 12 is 3×4. That is, if all
8 + 12 = 20 individuals in the population had been untreated, then 2 + 8 = 10
would have died. The denominator of the causal risk ratio, Pr[Y
a=0
= 1], is
10/20 = 0.5. The first tree in Figure 2.2 shows the population had everybody
22 Randomized experiments
remained untreated. Of course, these calculations rely on the condition that
treated individuals with L = 0, had they remained untreated, would have had
the same probability of death as those who actually remained untreated. This
condition is precisely exchangeability given L = 0.
The numerator of the causal risk ratio Pr[Y
a=1
= 1] is the counterfactual
risk of death had everybody in the population been treated. Reasoning as in
the previous paragraph, this risk is calculated to be also 10/20 = 0.5, under
exchangeability given L = 1. The second tree in Figure 2.2 shows the popu-
lation had everybody been treated. Combining the results from this and the
previous paragraph, the causal risk ratio Pr[Y
a=1
= 1]/ Pr[Y
a=0
= 1] is equal
to 0.5/0.5 = 1. We are done.
Let us examine how this method works. The two trees in Figure 2.2 are
a simulation of what would have happened had all individuals in the popula-
tion been untreated and treated, respectively. These simulations are correct
under conditional exchangeability. Both simulations can be pooled to create a
hypothetical population in which every individual appears as a treated and as
an untreated individual. This hypothetical population, twice as large as the
original population, is known as the pseudo-population. Figure 2.3 shows the
entire pseudo-population. Under conditional exchangeability Y
a
⊥⊥A|L in the
original population, the treated and the untreated are (unconditionally) ex-
changeable in the pseudo-population because the L is independent of A. That
is, the associational risk ratio in the pseudo-population is equal to the causal
risk ratio in both the pseudo-population and the original population.
Figure 2.3
This method is known as inverse probability (IP) weighting. To see why,
let us look at, say, the 4 untreated individuals with L = 0 in the populationIP weighted estimators were pro-
posed by Horvitz and Thompson
(1952) for surveys in which subjects
are sampled with unequal probabil-
ities. See Technical Point 12.1.
of Figure 2.1. These individuals are used to create 8 members of the pseudo-
population of Figure 2.3. That is, each of them receives a weight of 2, which
is equal to 1/0.5. Figure 2.1 shows that 0.5 is the conditional probability of
staying untreated given L = 0. Similarly, the 9 treated individuals with L = 1
2.4 Inverse probability weighting 23
Technical Point 2.2
Formal definition of IP weights. An individual’s IP weight depends on the individual’s values of treatment A and
covariate L. For example, a treated individual with L = l receives the weight 1/ Pr [A = 1|L = l], whereas an untreated
individual with L = l
′
receives the weight 1/ Pr [A = 0|L = l
′
]. We can express these weights using a single expression for
all individuals—regardless of their individual treatment and covariate values—by using the probability density function
(pdf) of A rather than the probability of A. The conditional pdf of A given L evaluated at the values a and l is
represented by f
A|L
[a|l], or simply as f [a|l]. For discrete variables A and L, f [a|l] is the conditional probability
Pr [A = a|L = l]. In a conditionally randomized experiment, f [a|l] is positive for all l such that Pr [L = l] is nonzero.
Since the denominator of the weight for each individual is the conditional density evaluated at the individual’s own
values of A and L, it can be expressed as the conditional density evaluated at the random arguments A and L (as
opposed to the fixed arguments a and l), that is, as f [A|L]. This notation, which appeared in Figure 2.3, is used to
define the IP weights W
A
= 1/f [A|L]. It is needed to have a unified notation for the weights because Pr [A = A|L = L]
is tautologically equal to 1 and thus not considered proper notation.
As explained in the main text, the mean of the outcome in the pseudo-population E
ps
[Y |A = a] equals the IP
weighted mean of the outcome in the population, E [Y I (A = a) / Pr (A = a|L)], where I (A = a) is 1 when A = a and
0 otherwise. A proof follows:
E
ps
[Y |A = a] = E
ps
[Y I (A = a)] / E
ps
[I (A = a)] (by the laws of probability)
= E
W
A
Y I (A = a)
/ E
I (A = a) W
A
(by definition of E
ps
)
= E [Y I (A = a) / Pr (A = a|L)] / E [I (A = a) / Pr (A = a|L)] (because I (A = a) /f (A|L) = I (A = a) /f (a|L))
= E [Y I (A = a) / Pr (A = a|L)] (because E [I (A = a) / Pr (A = a|L) |L] = 1).
in Figure 2.1 are used to create 12 members of the pseudo-population. That
is, each of them receives a weight of 1.33 = 1/0.75. Figure 2.1 shows that 0.75
is the conditional probability of being treated given L = 1. Informally, the
pseudo-population is created by weighting each individual in the population
by the inverse of the conditional probability of receiving the treatment levelIP weight: W
A
= 1/f [A|L]
that she indeed received. These IP weights are shown in Figure 2.3.
IP weighting yielded the same result as standardization—causal risk ratio
equal to 1— in our example above. This is no coincidence: standardization and
IP weighting are mathematically equivalent (see Technical Point 2.3). In fact,
both standardization and IP weighting can be viewed as procedures to build
a new tree in which all individuals receive treatment a. Each method uses a
different set of the probabilities to build the counterfactual tree: IP weighting
uses the conditional probability of treatment A given the covariate L (as shown
in Figure 2.1), standardization uses the probability of the covariate L and the
conditional probability of outcome Y given A and L.
Because both standardization and IP weighting simulate what would have
been observed if the variable (or variables in the vector) L had not been used
to decide the probability of treatment, we often say that these methods adjust
for L. In a slight abuse of language we sometimes say that these methods
control for L, but this “analytic control” is quite different from the “physical
control” in a randomized experiment. Standardization and IP weighting can
be generalized to conditionally randomized studies with continuous outcomes
(see Technical Point 2.3).
Why not finish this book here? We have a study design (an ideal random-
ized experiment) that, when combined with the appropriate analytic method
(standardization or IP weighting), allows us to compute average causal effects.
Unfortunately, randomized experiments are often unethical, impractical, or un-
timely. For example, it is questionable that an ethical committee would have
24 Randomized experiments
approved our heart transplant study. Hearts are in short supply and society
favors assigning them to individuals who are more likely to benefit from the
transplant, rather than assigning them randomly among potential recipients.
Also one could question the feasibility of the study even if ethical issues were
ignored: double-blind assignment is impossible, individuals assigned to medical
treatment may not resign themselves to forego a transplant, and there may not
be compatible hearts for those assigned to transplant. Even if the study were
feasible, it would still take several years to complete it, and decisions must be
made in the interim. Frequently, conducting an observational study is the least
bad option.
2.4 Inverse probability weighting 25
Technical Point 2.3
Equivalence of IP weighting and standardization. Assume that A is discrete with finite number of values and
that f [a|l] is positive for all l such that Pr [L = l] is nonzero. This positivity condition is guaranteed to hold in
conditionally randomized experiments. Under positivity, the standardized mean for treatment level a is defined as
P
l
E [Y |A = a, L = l] Pr [L = l] and the IP weighted mean of Y for treatment level a is defined as E
I (A = a) Y
f [A|L]
.
The indicator function I (A = a) is the function that takes value 1 for individuals with A = a, and 0 for the others.
We now prove the equality of the IP weighted and standardized means under positivity. By definition of expectation,
E
I (A = a) Y
f [A|L]
=
X
l
1
f [a|l]
{E [Y |A = a, L = l] f [a|l] Pr [L = l]} =
P
l
{E [Y |A = a, L = l] Pr [L = l]} where in
the final step we cancelled f [a|l] from the numerator and denominator, and in the first step we did not need to sum
over the possible values of A because for any a
′
other than a the quantity I(a
′
) is zero. The proof treats A and L as
discrete but not necessarily dichotomous. For continuous L simply replace the sum over L with an integral.
The proof makes no reference to counterfactuals. However, if we further assume conditional exchangeability, then
both the IP weighted and the standardized means are equal to the counterfactual mean E [Y
a
]. Here we provide two
different proofs of this last statement. First, we prove equality of E [Y
a
] and the standardized mean as in the text:
E [Y
a
] =
X
l
E [Y
a
|L = l] Pr [L = l] =
X
l
E [Y
a
|A = a, L = l] Pr [L = l] =
X
l
E [Y |A = a, L = l] Pr [L = l]
where the second equality is by conditional exchangeability and positivity, and the third by consistency. Second, we prove
equality of E [Y
a
] and the IP weighted mean as follows: E
I (A = a)
f [A|L]
Y
is equal to E
I (A = a)
f [A|L]
Y
a
by consistency.
Next, because positivity implies f [a|L] is never 0, we have
E
I (A = a)
f [A|L]
Y
a
= E
E
I (A = a)
f [a|L]
Y
a
L
= E
E
I (A = a)
f [a|L]
L
E [Y
a
|L]
(by conditional exchangeability)
= E {E [Y
a
|L]} (because E
I (A = a)
f [a|L]
L
= 1 ) = E [Y
a
] .
When treatment is continuous, which is an unlikely design choice in conditionally randomized experiments,
E [I (A = a) Y /f (A|L)] is no longer equal to
P
l
E [Y |A = a, L = l] Pr[L = l] and thus is biased for E [Y
a
] even
under exchangeability. To see this, one can calculate that E [I (A = a) /f (a|l) |L = l] is equal to 0 rather than 1 if
we take f (a|l) to be (a version of) the conditional density of A given L = l (with respect to Lebesgue measure). On
the other hand, if we continue to take f(a|l) to be Pr [A = a|L = l], the denominator f(a|L = l) is zero on a set
with probability 1 so positivity fails. In Section 12.4 we discuss how IP weighting can be generalized to accomodate
continuous treatments. In Technical Point 3.1, we discuss that the results above do not hold in the absence of positivity,
even for discrete A.
26 Randomized experiments
Chapter 3
OBSERVATIONAL STUDIES
Consider again the causal question “does one’s looking up at the sky make other pedestrians look up too?” After
considering a randomized experiment as in the previous chapter, you concluded that looking up so many times was
too time-consuming and unhealthy for your neck bones. Hence you decided to conduct the following study: Find
a nearby pedestrian who is standing in a corner and not looking up. Then find a second pedestrian who is walking
towards the first one and not looking up either. Observe and record their behavior during the next 10 seconds.
Repeat this process a few thousand times. You could now compare the proportion of second pedestrians who
looked up after the first pedestrian did, and compare it with the proportion of second pedestrians who looked up
before the first pedestrian did. Such a scientific study in which the investigator observes and records the relevant
data is referred to as an observational study.
If you had conducted the observational study described above, critics could argue that two pedestrians may both
look up not because the first pedestrian’s looking up causes the other’s looking up, but because they both heard
a thunderous noise above or some rain drops started to fall, and thus your study findings are inconclusive as to
whether one’s looking up makes others look up. These criticisms do not apply to randomized experiments, which is
one of the reasons why randomized experiments are central to the theory of causal inference. However, in practice,
the importance of randomized experiments for the estimation of causal effects is more limited. Many scientific
studies are not experiments. Much human knowledge is derived from observational studies. Think of evolution,
tectonic plates, global warming, or astrophysics. Think of how humans learned that hot coffee may cause burns.
This chapter reviews some conditions under which observational studies lead to valid causal inferences.
3.1 Identifiability conditions
Ideal randomized experiments can be used to identify and quantify average
causal effects because the randomized assignment of treatment leads to ex-
changeability. Take a marginally randomized experiment of heart transplant
and mortality as an example: if those who received a transplant had not re-
ceived it, they would have been expected to have the same death risk as thoseFor simplicity, this chapter consid-
ers only randomized experiments in
which all participants remain un-
der follow-up and adhere to their
assigned treatment throughout the
entire study. Chapters 8 and 9 dis-
cuss alternative scenarios.
who did not actually receive the heart transplant. As a consequence, an asso-
ciational risk ratio of 0.7 from the randomized experiment is expected to equal
the causal risk ratio.
Observational studies, on the other hand, may be much less convincing (for
an example, see the introduction to this chapter). A key reason for our hesita-
tion to endow observational associations with a causal interpretation is the lack
of randomized treatment assignment. As an example, take an observational
study of heart transplant and mortality in which those who received the heart
transplant were more likely to have a severe heart condition. Then, if those
who received a transplant had not received it, they would have been expected
to have a greater death risk than those who did not actually receive the heart
transplant. As a consequence, an associational risk ratio of 1.1 from the ob-
servational study would be a compromise between the truly beneficial effect of
transplant on mortality (which pushes the associational risk ratio to be under
1) and the underlying greater mortality risk in those who received transplant
28 Observational studies
(which pushes the associational risk ratio to be over 1). The best explanation
for an association between treatment and outcome in an observational study
is not necessarily a causal effect of the treatment on the outcome.
While recognizing that randomized experiments have intrinsic advantages
for causal inference, sometimes we are stuck with observational studies to an-
swer causal questions. What do we do? A common strategy is to analyze
our data as if treatment had been randomly assigned conditional on measured
covariates L—though we often know this is at best an approximation. Causal
inference from observational data then revolves around the hope that the ob-
servational study can be viewed as a conditionally randomized experiment.
Informally, an observational study can be conceptualized as a conditionally
randomized experiment if the following conditions hold:Table 3.1
L A Y
Rheia 0 0 0
Kronos 0 0 1
Demeter 0 0 0
Hades 0 0 0
Hestia 0 1 0
Poseidon 0 1 0
Hera 0 1 0
Zeus 0 1 1
Artemis 1 0 1
Apollo 1 0 1
Leto 1 0 0
Ares 1 1 1
Athena 1 1 1
Hephaestus 1 1 1
Aphrodite 1 1 1
Polyphemus 1 1 1
Persephone 1 1 1
Hermes 1 1 0
Hebe 1 1 0
Dionysus 1 1 0
1. the values of treatment under comparison correspond to well-defined in-
terventions that, in turn, correspond to the versions of treatment in the
data
2. the conditional probability of receiving every value of treatment, though
not decided by the investigators, depends only on measured covariates L
3. the probability of receiving every value of treatment conditional on L is
greater than zero, i.e., positive
In this chapter we describe these three conditions in the context of ob-
servational studies. Condition 1 was referred to as consistency in Chapter 1,
condition 2 was referred to as exchangeability in the previous chapters, and
condition 3 was referred to as positivity in Technical Point 2.3.
We will see that these conditions are often heroic, which explains why causal
inferences from observational studies are viewed with suspicion. However, if
the analogy between observational study and conditionally randomized exper-
iment happens to be correct, then we can use the methods described in the
previous chapter—IP weighting or standardization—to identify causal effects
from observational studies. We therefore refer to these conditions as identifi-
ability conditions or assumptions. For example, in the previous chapter, we
computed a causal risk ratio equal to 1 using the data in Table 2.2, which arose
from a conditionally randomized experiment. If the same data, now shown in
Table 3.1, had arisen from an observational study and the three identifiability
conditions above held true, we would also compute a causal risk ratio equal to
1.Rubin (1974, 1978) extended Ney-
man’s theory for randomized ex-
periments to observational studies.
Rosenbaum and Rubin (1983) re-
ferred to the combination of ex-
changeability and positivity as weak
ignorability, and to the combination
of full exchangeability (see Tech-
nical Point 2.1) and positivity as
strong ignorability.
Importantly, in ideal randomized experiments the identifiability conditions
hold by design. That is, for a conditionally randomized experiment, we would
only need the data in Table 3.1 to compute the causal risk ratio of 1. In
contrast, to identify the causal risk ratio from an observational study, we would
need to assume that the identifiability conditions held, which of course may not
be true. Causal inference from observational data requires two elements: data
and identifiability conditions. See Fine Point 3.1 for a more precise definition
of identifiability.
When any of the identifiability conditions does not hold, the analogy be-
tween observational study and conditionally randomized experiment breaks
down. In that situation, there are other possible approaches to causal inference
from observational data, which require a different set of identifiability condi-
tions. One of these approaches is hoping that a predictor of treatment, referred
to as an instrumental variable, behaves as if it had been randomly assigned con-
ditional on the measured covariates. We discuss instrumental variable methods
in Chapter 16.
3.2 Exchangeability 29
Fine Point 3.1
Identifiability of causal effects. We say that an average causal effect is (nonparametrically) identifiable under a
particular set of assumptions if these assumptions imply that the distribution of the observed data is compatible with
a single value of the effect measure. Conversely, we say that an average causal effect is nonidentifiable under the
assumptions when the distribution of the observed data is compatible with several values of the effect measure. For
example, if the study in Table 3.1 had arisen from a conditionally randomized experiment in which the probability of
receiving treatment depended on the value of L (and hence conditional exchangeability Y
a
⊥⊥A|L holds by design) then
we showed in the previous chapter that the causal effect is identifiable: the causal risk ratio equals 1, without requiring
any further assumptions. However, if the data in Table 3.1 had arisen from an observational study, then the causal risk
ratio equals 1 only if we supplement the data with the assumption of conditional exchangeability Y
a
⊥⊥A|L. To identify
the causal effect in observational studies, we need an assumption external to the data, an identifying assumption. In
fact, if we decide not to supplement the data with the identifying assumption, then the data in Table 3.1 are consistent
with a causal risk ratio
• lower than 1, if risk factors other than L are more frequent among the treated.
• greater than 1, if risk factors other than L are more frequent among the untreated.
• equal to 1, if all risk factors except L are equally distributed between the treated and the untreated or, equivalently,
if Y
a
⊥⊥A|L.
This chapter discusses the three identifiability conditions for nonparametric identification of average causal effects.
In Chapter 16, we describe alternative identifiability conditions which suffice for nonparametric identification of average
causal effects.
Not surprisingly, observational methods based on the analogy with a con-
ditionally randomized experiment have been traditionally privileged in disci-
plines in which this analogy is often reasonable (e.g., epidemiology), whereas
instrumental variable methods have been traditionally privileged in disciplines
in which observational studies cannot often be conceptualized as condition-
ally randomized experiments given the measured covariates (e.g., economics).
Until Chapter 16, we will focus on causal inference approaches that rely on
the ability of the observational study to emulate a conditionally randomized
experiment. We now describe in more detail each of the three identifiability
conditions.
3.2 Exchangeability
We have already said much about exchangeability Y
a
⊥⊥A. In marginally (i.e.,
unconditionally) randomized experiments, the treated and the untreated areAn independent predictor of the
outcome is a covariate associated
with the outcome Y within levels of
treatment. For dichotomous out-
comes, independent predictors of
the outcome are often referred to
as risk factors for the outcome.
exchangeable because the treated, had they remained untreated, would have
experienced the same average outcome as the untreated did, and vice versa.
This is so because randomization ensures that the independent predictors of
the outcome are equally distributed between the treated and the untreated
groups.
For example, take the study summarized in Table 3.1. We said in the pre-
vious chapter that exchangeability clearly does not hold in this study because
69% treated versus 43% untreated individuals were in critical condition L = 1
30 Observational studies
at baseline. This imbalance in the distribution of an independent outcome
predictor is not expected to occur in a marginally randomized experiment (ac-
tually, such imbalance might occur by chance but let us keep working under
the illusion that our study is large enough to prevent chance findings).
On the other hand, an imbalance in the distribution of independent out-
come predictors L between the treated and the untreated is expected by
design in conditionally randomized experiments in which the probability of
receiving treatment depends on L. The study in Table 3.1 is such a con-
ditionally randomized experiment: the treated and the untreated are not
exchangeable—because the treated had, on average, a worse prognosis at the
start of the study—but the treated and the untreated are conditionally ex-
changeable within levels of the variable L. In the subset L = 1 (critical con-
dition), the treated and the untreated are exchangeable because the treated,
had they remained untreated, would have experienced the same average out-
come as the untreated did, and vice versa. And similarly for the subset L = 0.
An equivalent statement: conditional exchangeability Y
a
⊥⊥A|L holds in condi-
tionally randomized experiments because, within levels of L, all other outcome
predictors are equally distributed between the treated and untreated groups.
Back to observational studies. When treatment is not randomly assigned
by the investigators, the reasons for receiving treatment are likely to be associ-
ated with some outcome predictors. That is, like in a conditionally randomized
experiment, the distribution of outcome predictors will generally vary between
the treated and untreated groups in an observational study. For example, theIn Chapter 7, we will refer to these
type of outcome predictors as con-
founders.
data in Table 3.1 could have arisen from an observational study in which doc-
tors tend to direct the scarce heart transplants to those who need them most,
i.e., individuals in critical condition L = 1. In fact, if the only outcome pre-
dictor that is unequally distributed between the treated and the untreated is
L, then one can refer to the study in Table 3.1 as either (i) an observational
study in which the probability of treatment A = 1 is 0.75 among those with
L = 1 and 0.50 among those with L = 0, or (ii) a (non blinded) conditionally
randomized experiment in which investigators randomly assigned treatment
A = 1 with probability 0.75 to those with L = 1 and 0.50 to those with L = 0.
Both characterizations of the study are logically equivalent. Under either char-
acterization, conditional exchangeability Y
a
⊥⊥A|L holds and standardization
or IP weighting can be used to identify the causal effect.
Of course, the crucial question for the observational study is whether L is
the only outcome predictor that is unequally distributed between the treated
and the untreated. Sadly, the question must remain unanswered, so our in-
vestigators need to be willing to work under the assumption that conditional
exchangeability Y
a
⊥⊥A|L holds. Also, note that not all variables that are un-
equally distributed between treatment groups need to be included in L. For
example, heart transplants are assigned to individuals with low probability of
rejecting the transplant, i.e., a heart with certain human leukocyte antigen
(HLA) genes will be assigned to an individual who happen to have compatible
genes. Because HLA genes are not predictors of mortality, conditional on L
and A, then treatment assignment is essentially random within levels of L and
thus HLA needs not be considered in the analysis.
In the absence of randomization, there is no guarantee that conditional ex-
changeability holds. For example, suppose that, unknown to the investigators,
doctors prefer to transplant hearts into nonsmokers. Consider two individuals
with L = 1. One of them is a smoker (U = 1) and the other one is a nonsmoker
(U = 0), the one with U = 1 has a lower probability of receiving treatment
A = 1. When the distribution of smoking, an important outcome predictor,
3.2 Exchangeability 31
Fine Point 3.2
Crossover randomized experiments. In Fine Point 2.1, we described crossover experiments in which an individual
is observed during two or more periods—say t = 0 and t = 1—and the individual receives a different treatment value
in each period. We showed that individual causal effects can be identified in crossover experiments when the following
three strong conditions hold: i) no carryover effect of treatment: Y
a
0
,a
1
it=1
= Y
a
1
it=1
, ii) the individual causal effect does
not depend on time: Y
a
t
=1
it
− Y
a
t
=0
it
= α
i
for t = 0, 1, and iii) the counterfactual outcome under no treatment does
not depend on time: Y
a
t
=0
it
= β
i
for t = 0, 1. No randomization was required. We now turn our attention to crossover
randomized experiments in which the order of treatment values that an individual receives is randomly assigned.
Randomized treatment assignment becomes important when, due to possible temporal effects, we do not assume iii)
holds. For simplicity, assume that every individual is randomized to either (A
i1
= 1, A
i0
= 0) or (A
i1
= 0, A
i0
= 1)
with probability 0.5. Let Y
a
1
=0
i1
− Y
a
0
=0
i0
= r
i
. Then, under i) and ii) and consistency, if A
i0
= 0 and A
i1
= 1,
then Y
i1
− Y
i0
= α
i
+ r
i
, and if A
i1
= 0 and A
i0
= 1, then Y
i0
− Y
i1
= α
i
− r
i
. Because r
i
is unknown we can
no longer identify individual causal effects but, since A
i1
and A
i0
are randomized and therefore independent of r
i
, the
mean of (Y
i1
− Y
i0
) A
i1
+ (Y
i0
− Y
i1
) A
i0
estimates the average causal effect, i.e., E [α
i
]. If we only assume i), then
this mean estimates the average of the average treament effects at times 0 and 1, i.e., (E [α
i1
] + E [α
i0
]) /2, where
α
it
= Y
a
t
=1
it
− Y
a
t
=0
it
.
In conclusion, if assumption 1) of no carryover effect holds, then a crossover experiment can be used to estimate
average causal effects. However, for the type of treatments and outcomes we study in this book, the assumption of no
carryover effect is implausible.
differs between the treated (with lower proportion of smokers U = 1) and theWe use U to denote unmeasured
variables. Because unmeasured
variables cannot be used for stan-
dardization or IP weighting, the
causal effect cannot be identified
when the measured variables L are
insufficient to achieve conditional
exchangeability.
untreated (with higher proportion of smokers) in the stratum L = 1, con-
ditional exchangeability given L does not hold. Importantly, collecting data
on smoking would not prevent the possibility that other imbalanced outcome
predictors, unknown to the investigators, remain unmeasured.
Thus exchangeability Y
a
⊥⊥A|L may not hold in observational studies. Specif-
ically, conditional exchangeability Y
a
⊥⊥A|L will not hold if there exist unmea-
sured independent predictors U of the outcome such that the probability of
receiving treatment A depends on U within strata of L. Worse yet, even if
conditional exchangeability Y
a
⊥⊥A|L held, the investigators cannot empiri-
cally verify that is actually the case. How can they check that the distribution
of smoking is equal in the treated and the untreated if they have not collected
data on smoking? What about all the other unmeasured outcome predictors
U that may also be differentially distributed between the treated and the un-
treated? When analyzing an observational study under conditional exchange-To verify conditional exchange-
ability, one needs to confirm
that Pr [Y
a
= 1|A = a, L = l] =
Pr [Y
a
= 1|A = a, L = l]. But this
is logically impossible because, for
individuals who do not receive
treatment a (A = a) the value of
Y
a
is unknown and so the right
hand side cannot be empirically
evaluated.
ability, we must hope that our expert knowledge guides us correctly to collect
enough data so that the assumption is at least approximately true.
Investigators can use their expert knowledge to enhance the plausibility
of the conditional exchangeability assumption. They can measure many rele-
vant variables L (e.g., determinants of the treatment that are also independent
outcome predictors), rather than only one variable as in Table 3.1, and then as-
sume that conditional exchangeability is approximately true within the strata
defined by the combination of all those variables L. Unfortunately, no mat-
ter how many variables are included in L, there is no way to test that the
assumption is correct, which makes causal inference from observational data
a risky task. The validity of causal inferences requires that the investigators’
expert knowledge is correct. This knowledge, encoded as the assumption of
exchangeability conditional on the measured covariates, supplements the data
in an attempt to identify the causal effect of interest.
32 Observational studies
3.3 Positivity
Some investigators plan to conduct an experiment to compute the average ef-
fect of heart transplant A on 5-year mortality Y . It goes without saying that
the investigators will assign some individuals to receive treatment level A = 1
and others to receive treatment level A = 0. Consider the alternative: the
investigators assign all individuals to either A = 1 or A = 0. That would be
silly. With all the individuals receiving the same treatment level, computing
the average causal effect would be impossible. Instead we must assign treat-
ment so that, with near certainty, some individuals will be assigned to each of
the treatment groups. In other words, we must ensure that there is a proba-
bility greater than zero—a positive probability—of being assigned to each of
the treatment levels. This is the positivity condition.
We did not emphasize positivity when describing experiments because pos-
itivity is taken for granted in those studies. In marginally randomized ex-
periments, the probabilities Pr [A = 1] and Pr [A = 0] are both positive byThe positivity condition is some-
times referred to as the experimen-
tal treatment assumption.
design. In conditionally randomized experiments, the conditional probabili-
ties Pr [A = 1|L = l] and Pr [A = 0|L = l] are also positive by design for all
levels of the variable L that are eligible for the study. For example, if the
data in Table 3.1 had arisen from a conditionally randomized experiment, the
conditional probabilities of assignment to heart transplant would have been
Pr [A = 1|L = 1] = 0.75 for those in critical condition and Pr [A = 1|L = 0] =
0.50 for the others. Positivity holds, conditional on L, because neither of
these probabilities is 0 (nor 1, which would imply that the probability of no
heart transplant A = 0 would be 0). Thus we say that there is positivity if
Pr [A = a|L = l] > 0 for all a involved in the causal contrast. Actually, this
definition of positivity is incomplete because, if our study population were re-
stricted to the group L = 1, then there would be no need to require positivity
in the group L = 0. Positivity is only needed for the values l that are presentPositivity: Pr [A = a|L = l] > 0
for all values l with Pr [L = l] = 0
in the population of interest.
in the population of interest.
In addition, positivity is only required for the variables L that are required
for exchangeability. For example, in the conditionally randomized experiment
of Table 3.1, we do not ask ourselves whether the probability of receiving
treatment is greater than 0 in individuals with blue eyes because the variable
“having blue eyes” is not necessary to achieve exchangeability between the
treated and the untreated. (The variable “having blue eyes” is not an inde-
pendent predictor of the outcome Y conditional on L and A, and was not even
used to assign treatment.) That is, the standardized risk and the IP weighted
risk are equal to the counterfactual risk after adjusting for L only; positivity
does not apply to variables that, like “having blue eyes”, do not need to be
adjusted for.
In observational studies, neither positivity nor exchangeability are guaran-
teed. For example, positivity would not hold if doctors always transplant a
heart to individuals in critical condition L = 1, i.e., if Pr [A = 0|L = 1] = 0,
as shown in Figure 3.1. A difference between the conditions of exchangeabil-
ity and positivity is that positivity can sometimes be empirically verified (see
Chapter 12). For example, if Table 3.1 corresponded to data from an observa-
tional study, we would conclude that positivity holds for L because there are
people at all levels of treatment (i.e., A = 0 and A = 1) in every level of L
(i.e., L = 0 and L = 1).Our discussion of standardization and IP weighting
in the previous chapter was explicit about the exchangeability condition, but
only implicitly assumed the positivity condition (explicitly in Technical Point
2.3). Our previous definitions of standardized risk and IP weighted risk are
3.4 Consistency: First, define the counterfactual outcome 33
actually only meaningful when positivity holds. To intuitively understand why
the standardized and IP weighted risk are not well-defined when the positiv-
ity condition fails, consider Figure 3.1. If there were no untreated individuals
(A = 0) with L = 1, the data would contain no information to simulate what
would have happened had all treated individuals been untreated because there
would be no untreated individuals with L = 1 that could be considered ex-
changeable with the treated individuals with L = 1. See Technical Point 3.1
for details.
Figure 3.1
3.4 Consistency: First, define the counterfactual outcome
Consistency means that the observed outcome for every treated individual
equals her outcome if she had received treatment, and that the observed out-
come for every untreated individual equals her outcome if she had remained
untreated, i.e., Y
a
= Y for every individual with A = a. This statement seems
so obviously true that some readers may be wondering whether there are any
situations in which consistency does not hold. After all, if I take aspirin A = 1
and I die (Y = 1), isn’t it the case that my counterfactual outcome Y
a=1
un-
der aspirin equals 1 by definition? The apparent simplicity of the consistencyRobins and Greenland (2000) ar-
gued that well-defined counterfac-
tuals, or mathematically equivalent
concepts, are necessary for mean-
ingful causal inference.
condition is deceptive. Let us unpack consistency by explicitly describing its
two main components: (1) a precise definition of the counterfactual outcomes
Y
a
via a detailed specification of the superscript a, and (2) the linkage of the
counterfactual outcomes to the observed outcomes. This section deals with the
first component of consistency.
The methodology for causal inference described in this book is licensed by
the existence of well-defined counterfactual outcomes Y
a
. If Y
a
is well-defined,
then the causal effect Pr [Y
a
= 1] −Pr [Y
a
= 1] is well-defined. A fundamental
question is then, how do we know that the counterfactuals are well defined?
The answer is straightforward when, as in randomized experiments with perfect
adherence to the study protocol, the interventions of interest are well defined
34 Observational studies
Technical Point 3.1
Positivity for standardization and IP weighting. We have defined the standardized mean for treatment level
a as
P
l
E [Y |A = a, L = l] Pr [L = l]. However, this expression can only be computed if the conditional quan-
tity E [Y |A = a, L = l] is well defined, which will be the case when the conditional probability Pr [A = a|L = l] is
greater than zero for all values l that occur in the population. That is, when positivity holds. (Note the statement
Pr [A = a|L = l] > 0 for all l with Pr [L = l] = 0 is effectively equivalent to f [a|L] > 0 with probability 1.) Therefore,
the standardized mean is defined as
X
l
E [Y |A = a, L = l] Pr [L = l] if Pr [A = a|L = l] > 0 for all l with Pr [L = l] = 0,
and is undefined otherwise. The standardized mean can be computed only if, for each value of the covariate L in the
population, there are some individuals that received the treatment level a.
The IP weighted mean E
I (A = a) Y
f [A|L]
is no longer equal to E
I (A = a) Y
f [a|L]
when positivity does not hold.
Specifically, E
I (A = a) Y
f [a|L]
is undefined because the undefined ratio
0
0
occurs in computing the expectation. On the
other hand, the IP weighted mean E
I (A = a) Y
f [A|L]
is always well defined since its denominator f [A|L] can never be
zero. However, it is now a biased estimate of the counterfactual mean even under exchangeability when positivity fails
to hold. In particular, E
I (A = a) Y
f [A|L]
is equal to Pr [L ∈ Q(a)]
P
l
E [Y |A = a, L = l, L ∈ Q(a)] Pr [L = l|L ∈ Q(a)]
where Q(a) = {l; Pr (A = a|L = l) > 0} is the set of values l for which A = a may be observed with positive probability.
Therefore, under exchangeability, E
I (A = a) Y
f [A|L]
equals E [Y
a
|L ∈ Q(a)] Pr [L ∈ Q(a)].
From the definition of Q(a), Q(0) cannot equal Q(1) when A is binary and positivity does not hold. In this case the
contrast E
I (A = 1) Y
f [A|L]
− E
I (A = 0) Y
f [A|L]
has no causal interpretation, even under exchangeability, because it is a
contrast between two different groups. Under positivity, Q(1) = Q(0) and the contrast is the average causal effect if
exchangeability holds.
themselves. Consider again a randomized experiment of heart transplant A and
5-year mortality Y . Before enrolling patients in the study, the investigators
wrote a protocol in which the two interventions of interest—heart transplant
a = 1 and medical therapy a = 0—were described in detail. For example, the
investigators specified that individuals assigned to heart transplant were to
receive certain pre-operative procedures, anesthesia, surgical technique, post-
operative care, and immunosuppressive therapy in an attempt to ensure that
each individual receives the same version of the treatment. Had the proto-
col not specified these details, it is possible that each doctor had conducted a
different version of the treatment “heart transplant”, perhaps using their pre-Fine Point 1.2 introduced the con-
cept of multiple versions of treat-
ment.
ferred surgical technique or immunosuppressive therapy. We define Y
a=1
as
the individual’s outcome in this study if the instructions for intervention a = 1
in the protocol of the experiment were followed, and analogously for Y
a=0
.
But how do we know that the counterfactual outcomes are well defined in
an observational study? Again, we will have well-defined counterfactuals if we
have well-defined interventions. To do so, we need to specify what intervention
is represented by a in Y
a
. For example, for an observational study on the
effect of heart transplant, we would specify the interventions of interest as for
3.4 Consistency: First, define the counterfactual outcome 35
Fine Point 3.3
On states and interventions. Variables like socioeconomic status or obesity define states, e.g., being poor, being
obese. Causal questions about changes in states are of the form “what if these individuals become poor or obese?”These
variables, however, are often not sufficiently well-defined for quantitative causal inference.
As an example, consider “the effect of becoming obese on myocardial infarction”
˙
(For simplicity, we use a traditional
definition of obesity as body mass index ≥ 30.) The quoted text does not have a meaningful interpretation because, as
discussed in the main text, the counterfactual outcome is ill-defined. One might think it would become well defined if we
specified the start and end of the intervention (e.g., age 40 years though age 50 years) and the procedure by which body
weight would be changed. However, if we specified all these details, we would not be describing the effect of obesity
but the effect of whatever interventions we are specifying. Hern´an and Taubman (2008) discuss the tribulations of two
world leaders—a despotic king and a clueless president—when considering “the effect of obesity“in their countries.
the randomized trial above, and for an observational study on the causal effect
of exercise, we would specify duration, frequency, intensity, type (swimming,
running...) and how the time devoted to exercise would otherwise be spent
(rehearsing with your band, watching television...). The difficulty of specifying
the treatment a increases for causal questions involving biological (e.g., blood
pressure, LDL-cholesterol, body weight) or social (e.g., socioeconomic status)
factors or states.
Take the effect of weight gain on fatal myocardial infarction. Suppose that,
on Zeus’s 35th birthday, we decided to make him gain 20 kilograms (kg) by
age 40 by lowering his daily exercise. He had a fatal myocardial infarction at
age 49. Now suppose that, in a parallel universe identical to ours, on Zeus’s
35th birthday we decided to make him gain 20 kg by age 40 by increasing his
caloric intake. He did not have a fatal myocardial infarction before age 50.
That is, in both universes Zeus gains 20 kg, but only in one of them he had a
fatal heart attack.
Because Zeus’s counterfactual outcome under weight gain of 20 kg can be
either death or no death, we conclude that specifying a = 1 as “weight gain of
20 kg” is too vague to define the counterfactual outcomes Y
a
. The problem is
that we can only change the value of weight gain by interventions (e.g., diet,
exercise) that may have effects on the outcome through causal pathways that
may not involve exclusively weight gain. See also Fine Point 3.3.Whether causal effects are ill-
defined depends on the outcome of
interest. Consider the effect of obe-
sity on job discrimination—as mea-
sured by the proportion of job ap-
plicants called for a personal in-
terview after the employer reviews
the applicant’s resume and photo-
graph. Here, the treatment is “obe-
sity as perceived by the employer”,
rather than “biological obesity”.
Therefore, the biological mecha-
nisms that led to obesity may be
irrelevant.
In contrast, if we were interested in the causal effect of a weight loss pill A on
mortality, this problem would not arise: “taking the pill” a = 1 is a well-defined
intervention because it does not require considering any other interventions
(e.g., on diet or exercise). Of course, the value of the counterfactual outcome
Y
a
can still depend on the individual’s values of any previous interventions
(e.g., on diet and exercise).
The more precisely we define the meaning of a = 1 and a = 0, the more
precise our causal questions are. However, absolute precision in the definition
of treatment is neither necessary nor possible. For example, for exercise, we
do not need to specify the direction of running (clockwise or counterclockwise)
around your neighborhood’s park. Scientists agree that the direction of running
is irrelevant because varying it would not lead to different outcomes. That is,
we only need sufficiently well-defined interventions a for which no meaningful
vagueness remains.
Which begs the question “how do we know that a treatment is sufficiently
well-defined?” Or, equivalently, how do we know that no meaningful vague-
36 Observational studies
Fine Point 3.4
Protocols open to interpretation. It is possible that Pr[Y
a=1
= 1] differs between two randomized experiments with
identical populations and protocols. To see this, consider the following scenario.
In both experiments, individuals assigned to a = 1 underwent a surgical operation according to the instructions in the
protocol. However, the protocol did not specify how to match patients with surgeons. In the first experiment, individuals
assigned to a = 1 were referred to and operated on by experienced surgeons if they were high risk patients, and by
less experienced surgeons if they were low risk patients. Because of this, almost no patients died and Pr[Y
a=1
= 1]
was close to 0. In contrast, in the second experiment, individuals assigned to a = 1 were referred to a surgeon without
regard to the patient’s risk and the surgeon’s experience. In this study Pr[Y
a=1
= 1] is far from zero because many
high-risk patients were operated on by inexperienced surgeons.
By definition, lack of exchangeability cannot explain the difference in Pr[Y
a=1
= 1] because both experiments were
randomized. Rather, the difference is explained by the different versions of treatment used in each trial. Because the
protocol did not specify how to match patients with surgeons, the two trials ended up with different results.
ness remains? The answer is “We don’t.” Declaring a treatment sufficiently
well-defined is a matter of agreement among experts based on the available
substantive knowledge. Today we agree that the direction of running is irrele-
vant, but future research might prove us wrong if it is demonstrated that, say,
leaning the body to the right, but not to the left, while running is harmful.
At any point in history, experts who write the protocols of randomized experi-
ments often attempt to eliminate as much vagueness as possible by employing
the subject-matter knowledge at their disposal. However, some vagueness is
inherent to all causal questions. The vagueness of causal questions can be re-
duced by a more detailed specification of treatment, but cannot be completely
eliminated.In pragmatic trials, the investiga-
tors may purposely choose not to
specify all components of the inter-
vention so that the treatment ver-
sions used in the trial reflect what
happens in real world settings.
Even the protocols of randomized experiments may fail to specify some rel-
evant components of the intervention. For example, the protocol of the above
heart transplant study did not specify the surgeon’s experience performing
heart transplants. Thus, both experienced and inexperienced surgeons partic-
ipated in the study. Because scant transplant experience is known to affect
post-transplant mortality, the risk Pr[Y
a=1
= 1] had all individuals received
treatment according to the protocol will depend on the unknown distribution
of experience of the participating surgeons. That is, the average causal effect
in a new community with a different distribution of surgical experience will
differ from the effect in the trial population, even if the new population follows
the exact same protocol as in the trial.
In fact, the value of Pr[Y
a=1
= 1], and therefore of the average causal
effect, may differ between two experiments conducted in the same population
and with the same protocol. This discrepancy would arise if the protocol
allows for a = 1 to include several versions of treatment with different causal
effects on the outcome of interest, and different versions of treatment are used
in each experiment. Fine Point 3.5 describes an example of two randomized
experiments with the same protocol but different causal effects. A different
distribution of versions of treatment affects the transportability of causal effects
(see Chapter 4). The same considerations apply to observational studies.
The discussion in this section illustrates an intrinsic feature of causal in-
ference: the articulation of causal questions is contingent on domain expertise
and informal judgment. What we view as a meaningful causal question at
present may turn out to be viewed as too vague in the future after learning
3.5 Consistency: Second, link counterfactuals to the observed data 37
Fine Point 3.5
Possible worlds. Philosophers of science have proposed counterfactual theories based on the concept of “possible
worlds” (Stalnaker 1968, Lewis 1973). The counterfactual Y
a
is defined to be the value of Y in the world in which
the individual received the treatment that is closest to the actual world. In particular, these philosophers assume that
Y
a
= Y if A = a because the closest possible world to the actual world is itself. Hence, under their definition of
counterfactuals, consistency always holds.
When A = a, the ”closest possible world” and thus the counterfactual Y
a
are always somewhat ill-defined and vague.
Nonetheless, Lewis noted that his definition of counterfactuals is often useful. Robins and Greenland (2000) agreed
but also argued that the concept of well-defined interventions should replace the concept of the closest possible world
because, in observational studies, counterfactuals are vague and ill-defined to the degree that one fails to make precise
the hypothetical interventions and causal contrasts under consideration.
that unspecified components of the treatment affect the outcome and thereforeThe phrase “no causation with-
out manipulation” (Holland 1986)
captures the idea that meaningful
causal inference requires sufficiently
well-defined interventions. How-
ever, bear in mind that sufficiently
well-defined interventions may not
be humanly feasible, or practicable,
interventions at a particular time
in history. For example, the effect
of genetic variants on disease was
considered sufficiently well defined
even before the existence of tech-
nology for genetic modification.
the magnitude of the causal effect. Years from now, scientists will probably
refine our obesity question in terms of cellular modifications which we barely
understand at this time. Again, the term sufficiently well-defined treatment
relies on expert consensus, which changes over time. Fine Point 3.4 links this
discussion with previous proposals.
Refining the causal question, until it is agreed that no meaningful vagueness
remains, is good practice for sound causal inference. For example, declaring
our interest in “the effect of obesity” may be viewed as just a starting point
for a discussion during which we will sharpen, and possibly modify, the causal
question by refining the specification of the treatment until, hopefully, a con-
sensus is reached with our colleagues. The more precisely we specify the treat-
ment, the better defined the causal question is and the fewer opportunities for
miscommunication between researchers and decision makers exist.
3.5 Consistency: Second, link counterfactuals to the observed data
As a reminder, the consistency condition says that Y
a
= Y for individuals
with A = a. In the previous section, we described the first component of
consistency: sufficiently well-defined counterfactual outcomes Y
a
such that
no meaningful vagueness remains. In this section, we describe the second
component of consistency in observational studies: ensuring that the equality
Y
a
= Y holds, i.e., linking the counterfactual outcomes to the observed data.For an expanded discussion of the
issues described in Sections 3.4 and
3.5, see the text and references in
Hern´an (2016), and in Robins and
Weissman (2016).
Suppose our goal is quantifying the effect of heart transplant a = 1 vs.
medical therapy a = 0 using observational data. We carefully specify the two
treatment versions a = 1 and a = 0 of interest. Experts agree that a = 1 and
a = 0 are sufficiently well-defined and, therefore, that no meaningful vagueness
remains in the specification of the counterfactual outcomes Y
a=1
and Y
a=0
.
Specifically, we specified that heart transplant a = 1 includes certain pre-
operative procedures, anesthesia, surgical technique, post-operative care, and
immunosuppressive therapy, as well as surgeons who had conducted at least 10
heart transplants in the last five years. Now suppose that, in our observational
data, all surgeons have conducted only between 5 and 9 heart transplants in
the last five years. Then, our carefully defined counterfactual outcome Y
a=1
cannot be linked to any of the observed outcomes Y because nobody in the
38 Observational studies
study population received the treatment version a = 1.
That is, the validity of the consistency condition is threatened by ill-defined
treatments like “weight gain” (previous section), but also by sufficiently well-
defined treatments like “heart transplant” that are absent in the data (this
section). This latter problem is the result of a lack of (unconditional) positivity
for the treatment of interest.
To link the counterfactual outcomes Y
a=1
and the observed outcomes Y ,
we have to ensure that only individuals receiving treatment version a = 1 are
considered as treated individuals (A = 1) in the analysis, and analogously
for the untreated. The implication is that, if we want to quantify the causal
effect Pr[Y
a=1
= 1] − Pr[Y
a=0
= 1] using observational data, we need data
in which some individuals received a = 1 and a = 0. Being able to describe
a well-defined intervention a, as we did, is not helpful if the intervention does
not occur in the observed data, i.e., if we cannot reasonably assume that the
equality Y
a
= Y holds for at least some individuals.
An obvious approach to handling the mismatch between the treatment
version of interest and the treatment versions in the observed data is to hy-
pothesize that the effects of those versions of treatment are identical—that is,
that there is treatment variation irrelevance (See Fine Point 1.2). In some
cases, this hypothesis may be a good approximation. For example, it might
be argued that no additional relevant experience is gained after performing 5
transplants and, thus, that we can use observational data in which all surgeons
conducted at least 5 transplants to correctly identify the effect of “heart trans-
plant” a = 1 under the protocol requirement that all surgeons had previously
performed at least 10 heart transplants.Assuming treatment variation irrel-
evance may also be reasonable for
some biological factors. For exam-
ple, if interested in the effect of
pharmacologically-induced changes
in blood pressure, investigators may
be willing to assume that the par-
ticular medication used to achieve
the change is not relevant.
In other cases, however, this assumption may not be reasonable. For ex-
ample, it would be hard to justify that the use of observational data in which
all surgeons had conducted only 1 transplant to correctly identify the effect of
“heart transplant” a = 1 under the protocol requirement that all surgeons had
previously performed at least 10 heart transplants.
Matching the intervention of interest a = 1 with the observed “treatment”
value A = 1, and therefore equating the counterfactual outcome Y
a=1
with
the observed outcome Y
A
= Y , requires collecting detailed data. Not only
is this information necessary to detect a mismatch between the treatment of
interest and the data at hand, but also to have an informed discussion about
whether the available versions of treatment can be used in lieu of the treatment
version of interest. In our heart transplant study in this section, if information
on surgeon experience was not collected, we would not be able to determine
whether the counterfactual Y
a=1
can be linked to the observed Y .Confusion often arises from the
common practice of using the same
letter to refer to the hypothetical
intervention a and to the observed
value A before enough information
exists to match a and A.
Because data on treatment versions are often unavailable in observational
studies, consistency is often compromised. Since achieving consistency is not
easy in observational studies, a good practice is to make our reasoning as
transparent as possible, so that others can directly challenge our arguments.
The next section describes a procedure to achieve that transparency.
3.6 The target trial
The average causal effect is a contrast between mean counterfactual outcomes
under different treatment values. Because the counterfactual outcomes need
to be well defined, we can imagine a (hypothetical) randomized experiment to
quantify the causal effect of interest. We refer to that hypothetical experiment
3.6 The target trial 39
as the target experiment or the target trial. When conducting the target trialThe target trial—or its logical
equivalents—has long been cen-
tral to the causal inference frame-
work. Dorn (1953), Wold (1954),
Cochran (1972), Rubin (1974), Fe-
instein (1971), and Dawid (2000)
used the concept. Robins (1986)
generalized it for time-varying
treatments.
is not feasible, ethical, or timely, we resort to causal analyses of observational
data. Generally, one can view these observational analyses as an attempt to
emulate some target trial. If the emulation were successful, there would be
no difference between the results from the observational study and from the
target trial (had it been conducted).
In this chapter, we have explored three conditions—exchangeability, pos-
itivity, consistency—that help equate an observational study with a (con-
ditionally randomized) target experiment. When these conditions hold, we
can apply the methods described in the previous chapter—IP weighting or
standardization—to compute causal effects from the observational data.Fine Point 3.6 describes how to use
observational data to compute the
proportion of cases attributable to
treatment.
Therefore “what randomized experiment are you trying to emulate?” can
be a key question for causal inference from observational data. For each causal
effect that we wish to estimate using observational data, we may (i) specify
the target trial that we would like to, but cannot, conduct, and (ii) describe
how the observational data can be used to emulate that target trial. Specifying
the target trial, and therefore the causal effect of interest, requires specifying
key components of the trial’s protocol: eligibility criteria, interventions (or, in
general, treatment strategies), assignment, outcomes, start and end of follow-Hern´an and Robins (2016) speci-
fied the key components of the tar-
get trial. The acronym PICO (Pop-
ulation, Intervention, Comparator,
Outcome) is sometimes used to
summarize some of those compo-
nents (Richardson et al. 1995).
up, and causal contrasts.
Therefore, a valid emulation of the target trial requires that the observa-
tional dataset includes sufficient information to identify eligible individuals,
assign them to groups defined by the interventions they receive, and ascer-
tain their outcomes during the follow-up. For example, to estimate the causal
effect of heart transplant, we first specify the components of the protocol of
the target trial, and then try to emulate each of them using the observational
data. Such explicit emulation of a target trial improves causal inference from
observational data by making the interventions, and therefore the causal ques-
tion, well-defined (see Chapter 22 for an extended discussion of the target trial
framework). Once the causal question is well-defined via a target trial, investi-
gators can focus on whether and how conditional exchangeability across groups
can be achieved.When we are concerned that as-
suming conditional exchangeability
may not be reasonable given the
available data, we can consider
alternative identifying assumptions
(see Chapter 16) or perform sensi-
tivity analyses.
All of the above assumes that the interventions of interest are sufficiently
well-defined to translate them into a hypothetical experiment. But what can
we do when, based on current scientific knowledge, the causal question cannot
be translated into a target trial? As an example, consider “the causal effect
of weight loss” on mortality in individuals who are obese and do not smoke
at age 40. Because this causal question is somewhat vague, we replace it by
one that specifies the actual intervention that would be implemented to bring
about weight loss. For example, we could specify and emulate a target trial
about inducing weight loss via, say, exercise or diet.
In contrast to the conceptualization of causal inference from observational
data as a target trial emulation, some authors view “the causal effect of A on
Y ” as a well-defined quantity regardless of what A and Y stand for (as long as
A temporally precedes Y ). Often the argument goes like this:For some examples of this point of
view, see Pearl (2009), Schwartz
et al (2016), and Glymour and
Spiegelman (2016).
Requiring well-defined counterfactual outcomes via a target trial
imposes severe restrictions on the causal questions that can be
asked. Suppose we study weight loss and heart disease using ob-
servational data. We may not be able to characterize precisely the
causal effect of weight loss, but is that really so important if indeed
some causal effect exists? There is value in learning that many
deaths can be prevented if obese people, somehow, lost weight,
40 Observational studies
Fine Point 3.6
Attributable fraction. We have described effect measures like the causal risk ratio Pr[Y
a=1
= 1]/ Pr[Y
a=0
= 1] and
the causal risk difference Pr[Y
a=1
= 1] −Pr[Y
a=0
= 1], which compare the counterfactual risk under treatment a = 1
with the counterfactual risk under treatment a = 0. However, one could also be interested in measures that compare
the observed risk with the counterfactual risk under either treatment a = 1 or a = 0. This latter contrast allows us
to compute the proportion of cases that are attributable to treatment in an observational study, i.e., the proportion of
cases that would not have occurred had treatment not occurred. For example, suppose that all 20 individuals in our
population attended a dinner in which they were served either ambrosia (A = 1) or nectar (A = 0). The following day,
7 of the 10 individuals who received A = 1, and 1 of the 10 individuals who received A = 0, were sick. For simplicity,
assume exchangeability of the treated and the untreated so that the causal risk ratio is 0.7/0.1 = 7 and the causal
risk difference is 0.7 − 0.1 = 0.6. (In conditionally randomized experiments, one would compute these effect measures
via standardization or IP weighting.) It was later discovered that the ambrosia had been contaminated by a flock of
doves, which explains the increased risk summarized by both the causal risk ratio and the causal risk difference. We
now address the question ‘what fraction of the cases was attributable to consuming ambrosia?’
In this study we observed 8 cases, i.e., the observed risk was Pr [Y = 1] = 8/20 = 0.4. The risk that would have
been observed if everybody had received a = 0 is Pr[Y
a=0
= 1] = 0.1. The difference between these two risks is
0.4 − 0.1 = 0.3. That is, there is an excess 30% of the individuals who did fall ill but would not have fallen ill if
everybody in the population had received a = 0 rather than their treatment A. Because 0.3/0.4 = 0.75, we say that
75% of the cases are attributable to treatment a = 1: compared with the 8 observed cases, only 2 cases would have
occurred if everybody had received a = 0. This excess fraction or attributable fraction is defined as
Pr [Y = 1] − Pr[Y
a=0
= 1]
Pr [Y = 1]
See Fine Point 5.4 for a discussion of the excess fraction in the context of the sufficient-component-cause framework.
The excess fraction is generally different from the etiologic fraction , another version of the attributable fraction which
is defined as the proportion of cases mechanically caused by exposure. For example, suppose the untreated (A = 0)
would have had 7 cases if they have been treated, but these 7 cases would not have contained the 1 untreated case that
actually occurred, i.e., treatment produces 7 cases but prevents 1 case. Also suppose that, if untreated, the treated
would have had only 1 case but different from the 7 cases they actually had. Then the excess fraction would not be
equal to the etiologic fraction. Here the excess fraction is a lower bound on the etiologic fraction. Because the etiologic
fraction does not rely on the concept of excess cases, it can only be computed in randomized experiments under strong
assumptions. See Greenland and Robins, 1988 and Robins and Greenland, 1989.
even if the intervention required for achieving that transformation
is unspecified.
This is an appealing argument, but it is problematic for two reasons.
First, unspecified interventions may be unreasonable or impractical. For
example, suppose that some investigators are interested in learning about the
health effects of weight loss, but they do not propose and explicitly emulate
a target trial. Rather, they conduct a simplified analysis that compares the
risk of death in obese versus non-obese individuals at age 40. That comparison
corresponds implicitly to a target trial in which obese individuals are instanta-
neously transformed into individuals with a body mass index of 25 at baseline
(through a massive liposuction?). Such target trial cannot be emulated be-
cause very few people, if anyone, undergo such drastic instantaneous change
in the real world, and thus the counterfactual outcomes cannot generally be
linked to the observed outcomes. Had this draconian intervention been made
explicit, all scientists, including those who conducted the data analyses, would
3.6 The target trial 41
have agreed that consistency does not hold. Explicit target trial emulationExtreme or impossible interventions
are more likely to go unrecognized
when they are not explicitly speci-
fied.
prevents investigators from making implicit consistency assumptions that do
not cohere with their own beliefs.
In fact, anchoring observational data analyses to a target trial not only
helps sharpen the causal question and, but also makes the causal inference
more relevant for decision makers. This is the case even if the available data are
insufficient to emulate a contrast of well-defined interventions. For example, we
may not have sufficient data to emulate an intervention that precisely specifies
the method used to lose weight (e.g., diet, exercise, a pill), but we may have
sufficient data to ensure that other components of the intervention remain
realistic. If we had longitudinal data on body weight, we can specify a target
trial in which some individuals are assigned to lose 5% of body mass index
every year, starting at age 40 and for as long as their body mass index stays
over 25 (Part III of this book revolves around interventions that, like this
one, are sustained over time.) Though this intervention is not yet well-defined
(because it does not specify how the weight loss is achieved), it at least avoids
mandating an instantaneous weight loss, which corresponds to an intervention
that is impossible to implement. That we may not be able to define well-defined
counterfactual outcomes is no excuse to try to make them as less ill-defined as
possible.Danaei et al. (2016) tried to esti-
mate the effect of weight loss using
observational data. They left un-
specified the method used to lose
weight, but they carefully specified
the timing of the weight loss over
many years.
Second, unspecified interventions make it harder to achieve exchangeabil-
ity and positivity. Because the set of covariates L that result in conditional
exchangeability may vary across interventions, the usual uncertainty regard-
ing conditional exchangeability in observational studies is greatly exacerbated
if we forgo characterizing the interventions as well as possible. Also, if the
interventions remain unspecified, it is hard to characterize the combinations
of values of L that would make it impossible to receive the intervention in
the observational data, which increases the risk of an inadvertent violation of
positivity.
So what can we do when a target trial cannot be reasonably specified and
emulated or, more generally, when the counterfactual outcomes are not suffi-
ciently well defined? In those settings, observational data may still be quite
useful for non-causal prediction. That obese individuals have a higher mor-For an extended discussion about
the differences between prediction
and causal inference, which is a
form of counterfactual prediction,
see Hern´an, Hsu, and Healy (2019).
tality risk than nonobese individuals means that obesity is a predictor of—is
associated with—mortality. This is an important piece of information to iden-
tify individuals at high risk of mortality. By saying that obesity predicts—is
associated with—mortality, we remain causally agnostic: obesity might pre-
dict mortality in the sense that cigarette smoking predicts lung cancer or in
the sense that carrying a lighter predicts lung cancer. Thus the association
between obesity and mortality is an interesting hypothesis-generating exer-
cise and a motivation for further research (why does obesity predict mortality
anyway?), while acknowledging the magnitude of the association does not nec-
essarily correspond to that of a causal effect.
42 Observational studies
Chapter 4
EFFECT MODIFICATION
So far we have focused on the average causal effect in an entire population of interest. However, many causal
questions are about subsets of the population. Consider again the causal question “does one’s looking up at
the sky make other pedestrians look up too?” You might be interested in computing the average causal effect of
treatment—your looking up to the sky— in city dwellers and visitors separately, rather than the average effect in
the entire population of pedestrians.
The decision whether to compute average effects in the entire population or in a subset depends on the inferential
goals. In some cases, you may not care about the variations of the effect across different groups of individuals.
For example, suppose you are a policy maker considering the possibility of implementing a nationwide water
fluoridation program. Because this public health intervention will reach all households in the population, your
primary interest is in the average causal effect in the entire population, rather than in particular subsets. You will
be interested in characterizing how the causal effect varies across subsets of the population when the intervention
can be targeted to different subsets, or when the findings of the study need to be applied to other populations.
This chapter emphasizes that there is not such a thing as the causal effect of treatment. Rather, the causal
effect depends on the characteristics of the particular population under study.
4.1 Heterogeneity of treatment effects
We started this book by computing the average causal effect of heart trans-Table 4.1
V Y
0
Y
1
Rheia 1 0 1
Demeter 1 0 0
Hestia 1 0 0
Hera 1 0 0
Artemis 1 1 1
Leto 1 0 1
Athena 1 1 1
Aphrodite 1 0 1
Persephone 1 1 1
Hebe 1 1 0
Kronos 0 1 0
Hades 0 0 0
Poseidon 0 1 0
Zeus 0 0 1
Apollo 0 1 0
Ares 0 1 1
Hephaestus 0 0 1
Polyphemus 0 0 1
Hermes 0 1 0
Dionysus 0 1 0
plant A on death Y in a population of 20 members of Zeus’s extended family.
We used the data in Table 1.1, whose columns show the individual values
of the (generally unobserved) counterfactual outcomes Y
a=0
and Y
a=1
. Af-
ter examining the data in Table 1.1, we concluded that the average causal
effect was null. Half of the members of the population would have died if
everybody had received a heart transplant, Pr[Y
a=1
= 1] = 10/20 = 0.5,
and half of the members of the population would have died if nobody had re-
ceived a heart transplant, Pr[Y
a=0
= 1] = 10/20 = 0.5. The causal risk ratio
Pr[Y
a=1
= 1]/ Pr[Y
a=0
= 1] was 0.5/0.5 = 1 and the causal risk difference
Pr[Y
a=1
= 1] − Pr[Y
a=0
= 1] was 0.5 − 0.5 = 0.
We now consider two new causal questions: What is the average causal
effect of A on Y in women? And in men? To answer these questions we
will use Table 4.1, which contains the same information as Table 1.1 plus an
additional column with an indicator V for sex: V = 1 for females (referred
to as women in this book) and V = 0 for males (referred to as men). For
convenience, we have rearranged the table so that women occupy the first 10
rows, and men the last 10 rows.
Let us first compute the average causal effect in women. To do so, we need
to restrict the analysis to the first 10 rows of the table with V = 1. In this
subset of the population, the risk of death under treatment is Pr[Y
a=1
= 1|V =
1] = 6/10 = 0.6 and the risk of death under no treatment is Pr[Y
a=0
= 1|V =
1] = 4/10 = 0.4. The causal risk ratio is 0.6/0.4 = 1.5 and the causal risk
difference is 0.6 − 0.4 = 0.2. That is, on average, heart transplant A increases
44 Effect modification
the risk of death Y in women.
Let us next compute the average causal effect in men. To do so, we need
torestrict the analysis to the last 10 rows of the table with V = 0. In this subsetOur use of the terms “man” and
“woman” in this chapter can be
viewed as a slight abuse of notation
because these deities are gods and
goddesses, not men and women.
of the population, the risk of death under treatment is Pr[Y
a=1
= 1|V = 0] =
4/10 = 0.4 and the risk of death under no treatment is Pr[Y
a=0
= 1|V = 0] =
6/10 = 0.6. The causal risk ratio is 0.4/0.6 = 2/3 and the causal risk difference
is 0.4 −0.6 = −0.2. That is, on average, heart transplant A decreases the risk
of death Y in men.
Our example shows that a null average causal effect in the population does
not imply a null average causal effect in a particular subset of the population.
In Table 4.1, the null hypothesis of no average causal effect is true for the
entire population, but not for men or women when taken separately. It just
happens that the average causal effects in men and in women are of equal
magnitude but in opposite direction. Because the proportion of each sex is
50%, both effects cancel out exactly when considering the entire population.
Although exact cancellation of effects is probably rare, heterogeneity of the
individual causal effects of treatment is often expected because of variations in
individual susceptibilities to treatment. An exception occurs when the sharp
null hypothesis of no causal effect is true. Then no heterogeneity of effects
exists because the effect is null for every individual and thus the average causal
effect in any subset of the population is also null.
We are now ready to provide a definition of effect modifier. We say that V
is a modifier of the effect of A on Y when the average causal effect of A on YSee Section 6.6 for a structural clas-
sification of effect modifiers. varies across levels of V . Since the average causal effect can be measured using
different effect measures (e.g., risk difference, risk ratio), the presence of effect
modification depends on the effect measure being used. For example, sex VAdditive effect modification:
E[Y
a=1
− Y
a=0
|V = 1] =
E[Y
a=1
− Y
a=0
|V = 0]
is an effect modifier of the effect of heart transplant A on mortality Y on the
additive scale because the causal risk difference varies across levels of V . Sex
V is also an effect modifier of the effect of heart transplant A on mortality Y
on the multiplicative scale because the causal risk ratio varies across levels ofMultiplicative effect modification:
E[Y
a=1
|V =1]
E[Y
a=0
|V =1]
=
E[Y
a=1
|V =0]
E[Y
a=0
|V =0]
We do not consider effect modifica-
tion on the odds ratio scale because
the odds ratio is rarely, if ever, the
parameter of interest for causal in-
ference.
V . We only consider variables V that are not affected by treatment A as effect
modifiers.
In Table 4.1 the causal risk ratio is greater than 1 in women (V = 1) and
less than 1 in men (V = 0). Similarly, the causal risk difference is greater
than 0 in women (V = 1) and less than 0 in men (V = 0). That is, there is
qualitative effect modification because the average causal effects in the subsets
V = 1 and V = 0 are in the opposite direction. In the presence of qualitative
effect modification, additive effect modification implies multiplicative effect
modification, and vice versa. In the absence of qualitative effect modification,
however, one can find effect modification on one scale (e.g., multiplicative) but
not on the other (e.g., additive). To illustrate this point, suppose that, in a
second study, we computed the quantities shown to the left of this line. InMultiplicative, but not additive, ef-
fect modification by V :
Pr[Y
a=0
= 1|V = 1] = 0.8
Pr[Y
a=1
= 1|V = 1] = 0.9
Pr[Y
a=0
= 1|V = 0] = 0.1
Pr[Y
a=1
= 1|V = 0] = 0.2
this study, there is no additive effect modification by V because the causal
risk difference among individuals with V = 1 equals that among individuals
with V = 0, i.e., 0.9 − 0.8 = 0.1 = 0.2 − 0.1. However, in this study there
is multiplicative effect modification by V because the causal risk ratio among
individuals with V = 1 differs from that among individuals with V = 0, i.e.,
0.9/0.8 = 1.1 = 0.2/0.1 = 2. Since one cannot generally state that there is, or
there is not, effect modification without referring to the effect measure being
used (e.g., risk difference, risk ratio), some authors use the term effect-measure
modification, rather than effect modification, to emphasize the dependence of
the concept on the choice of effect measure.
4.2 Stratification to identify effect modification 45
4.2 Stratification to identify effect modification
A stratified analysis is the natural way to identify effect modification. To
determine whether V modifies the causal effect of A on Y , one computes the
causal effect of A on Y in each level (stratum) of the variable V . In theStratification: the causal effect of
A on Y is computed in each stra-
tum of V . For dichotomous V , the
stratified causal risk differences are:
Pr[Y
a=1
= 1|V = 1]−
Pr[Y
a=0
= 1|V = 1]
and
Pr[Y
a=1
= 1|V = 0]−
Pr[Y
a=0
= 1|V = 0]
previous section, we used the data in Table 4.1 to compute the causal effect
of transplant A on death Y in each of the two strata of sex V . Because
the causal effect differed between the two strata (on both the additive and the
multiplicative scale), we concluded that there was (additive and multiplicative)
effect modification by V of the causal effect of A on Y .
But the data in Table 4.1 are not the typical data one encounters in real
life. Instead of the two columns with each individual’s counterfactual outcomes
Y
a=1
and Y
a=0
, one will find two columns with each individual’s treatment
level A and observed outcome Y . How does the unavailability of the counter-
factual outcomes affect the use of stratification to detect effect modification?
The answer depends on the study design.
Consider first an ideal marginally randomized experiment. In Chapter 2
we demonstrated that, leaving aside random variability, the average causal ef-
fect of treatment can be computed using the observed data. For example, the
causal risk difference Pr[Y
a=1
= 1] − Pr[Y
a=0
= 1] is equal to the observed
associational risk difference Pr[Y = 1|A = 1] − Pr[Y = 1|A = 0]. The sameTable 4.2
Stratum V = 0
L A Y
Cybele 0 0 0
Saturn 0 0 1
Ceres 0 0 0
Pluto 0 0 0
Vesta 0 1 0
Neptune 0 1 0
Juno 0 1 1
Jupiter 0 1 1
Diana 1 0 0
Phoebus 1 0 1
Latona 1 0 0
Mars 1 1 1
Minerva 1 1 1
Vulcan 1 1 1
Venus 1 1 1
Seneca 1 1 1
Proserpina 1 1 1
Mercury 1 1 0
Juventas 1 1 0
Bacchus 1 1 0
reasoning can be extended to each stratum of the variable V because, if treat-
ment assignment was random and unconditional, exchangeability is expected
in every subset of the population. Thus the causal risk difference in women,
Pr[Y
a=1
= 1|V = 1] − Pr[Y
a=0
= 1|V = 1], is equal to the associational risk
difference in women, Pr[Y = 1|A = 1, V = 1] − Pr[Y = 1|A = 0, V = 1]. And
similarly for men. Thus, to identify effect modification by V in an ideal exper-
iment with unconditional randomization, one just needs to conduct a stratified
analysis, i.e., to compute the association measure in each level of the variable
V . Stratification can be used to compute average causal effects in subsets of
the population, but not individual effects (see Fine Points 2.1 and 3.2).
Consider now an ideal randomized experiment with conditional randomiza-
tion. In a population of 40 people, transplant A has been randomly assigned
with probability 0.75 to those in severe condition (L = 1), and with probabil-
ity 0.50 to the others (L = 0). The 40 individuals can be classified into two
nationalities according to their passports: 20 are Greek (V = 1) and 20 are
Roman (V = 0). The data on L, A, and death Y for the 20 Greeks are shown
in Table 2.2 (same as Table 3.1). The data for the 20 Romans are shown in
Table 4.2. The population risk under treatment, Pr[Y
a=1
= 1], is 0.55, and
the population risk under no treatment, Pr[Y
a=0
= 1], is 0.40. (Both risks
are readily calculated by using either standardization or IP weighting. We
leave the details to the reader.) The average causal effect of transplant A
on death Y is therefore 0.55 − 0.40 = 0.15 on the risk difference scale, and
0.55/0.40 = 1.375 on the risk ratio scale. In this population, heart transplant
increases the mortality risk.
As discussed in the previous chapter, the calculation of the causal effect
would have been the same if the data had arisen from an observational study
in which we believe that conditional exchangeability Y
a
⊥⊥A|L holds.
We now discuss how to conduct a stratified analysis to investigate whether
nationality V modifies the effect of A on Y . The goal is to compute the causal
effect of A on Y in the Greeks, Pr[Y
a=1
= 1|V = 1]−Pr[Y
a=0
= 1|V = 1], and
in the Romans, Pr[Y
a=1
= 1|V = 0] −Pr[Y
a=0
= 1|V = 0]. If these two causal
risk differences differ, we will say that there is additive effect modification by
46 Effect modification
Fine Point 4.1
Effect in the treated. This chapter is concerned with average causal effects in subsets of the population. One particular
subset is the treated (A = 1). The average causal effect in the treated is not null if Pr[Y
a=1
= 1|A = 1] = Pr[Y
a=0
=
1|A = 1] or, by consistency, if
Pr[Y = 1|A = 1] = Pr[Y
a=0
= 1|A = 1].
That is, there is a causal effect in the treated if the observed risk among the treated individuals does not equal the
counterfactual risk had the treated individuals been untreated. The causal risk difference in the treated is Pr[Y = 1|A =
1] − Pr[Y
a=0
= 1|A = 1]. The causal risk ratio in the treated, also known as the standardized morbidity ratio (SMR),
is Pr[Y = 1|A = 1]/ Pr[Y
a=0
= 1|A = 1]. The causal risk difference and risk ratio in the untreated are analogously
defined by replacing A = 1 by A = 0. Figure 4.1 shows the groups that are compared when computing the effect in the
treated and the effect in the untreated.
The average effect in the treated will differ from the average effect in the population if the distribution of individual
causal effects varies between the treated and the untreated. That is, when computing the effect in the treated, treatment
group A = 1 is used as a marker for the factors that are truly responsible for the modification of the effect between
the treated and the untreated groups. However, even though one could say that there is effect modification by the
pre-treatment variable V even if V is only a surrogate (e.g., nationality) for the causal effect modifiers, one would not
say that there is modification of the effect A by treatment A because it sounds confusing. The effect modification is
by unidentified variables that have a different distribution between the treatment groups.
See Section 6.6 for a graphical representation of true and surrogate effect modifiers. The bulk of this book is focused
on the causal effect in the population because the causal effect in the treated, or in the untreated, cannot be directly
generalized to time-varying treatments (see Part III).
V . And similarly for the causal risk ratios if interested in multiplicative effect
modification.
The procedure to compute the conditional risks Pr[Y
a=1
= 1|V = v] and
Pr[Y
a=0
= 1|V = v] in each stratum v has two stages: 1) stratification by
V , and 2) standardization by L (or, equivalently, IP weighting with weights
depending on L). We computed the standardized risks in the Greek stratumStep 2 can be ignored when V is
equal to the variables L that are
needed for conditional exchange-
ability (see Section 4.4).
(V = 1) in Chapter 2: the causal risk difference was 0 and the causal risk
ratio was 1. Using the same procedure in the Roman stratum (V = 0), we can
compute the risks Pr[Y
a=1
= 1|V = 0] = 0.6 and Pr[Y
a=0
= 1|V = 0] = 0.3.
(Again, we leave the details to the reader.) Therefore, the causal risk difference
is 0.3 and the causal risk ratio is 2 in the stratum V = 0. Because these effect
measures differ from those in the stratum V = 1, we say that there is both
additive and multiplicative effect modification by nationality V of the effect of
transplant A on death Y . This effect modification is not qualitative because
the effect is harmful or null in both strata V = 0 and V = 1.
We have shown that, in our study population, nationality V modifies the
effect of heart transplant A on the risk of death Y . However, we have made no
claims about the causal mechanisms involved in such effect modification. In
fact, it is possible that nationality is simply a marker for the causal factor that
is truly responsible for the modification of the effect. For example, suppose
that the quality of heart surgery is better in Greece than in Rome. One would
then find effect modification by nationality. An intervention to improve the
quality of heart surgery in Rome could eliminate the modification of the causal
effect by passport-defined nationality. Whenever we want to emphasize thisSee Section 6.6 for a graphical rep-
resentation of surrogate and causal
effect modifiers.
distinction, we will refer to nationality as a surrogate effect modifier , and to
quality of care as a causal effect modifier.
Therefore, our use of the term effect modification by V does not necessarily
4.3 Why care about effect modification 47
imply that V plays a causal role in the modification of the effect. To avoid
potential confusions, some authors prefer to use the more neutral term “effect
heterogeneity across strata of V ” rather than “effect modification by V .” The
next chapter introduces “interaction,” a concept related to effect modification,
that does attribute a causal role to the variables involved.
Figure 4.1
4.3 Why care about effect modification
There are several related reasons why investigators are interested in identifying
effect modification, and why it is important to collect data on pre-treatment
descriptors V even in randomized experiments.
First, if a factor V modifies the effect of treatment A on the outcome Y
then the average causal effect will differ between populations with different
prevalence of V . For example, the average causal effect in the population of
Table 4.1 is harmful in women and beneficial in men, i.e., there is qualitative
effect modification. Because there are 50% of individuals of each sex and the
sex-specific harmful and beneficial effects are equal but of opposite sign, the
average causal effect in the entire population is null. However, had we con-
ducted our study in a population with a greater proportion of women (e.g.,
graduating college students), the average causal effect in the entire population
would have been harmful. In the presence of non-qualitative effect modifica-
tion, the magnitude, but not the direction, of the average causal effect may
vary across populations. As examples of non-qualitative effect modification,
consider the effects of asbestos exposure (which differ between smokers and
nonsmokers) and of universal health care (which differ between low-income
and high-income families).
That is, the average causal effect in a population depends on the distribu-
tion of individual causal effects in the population. There is generally no such
a thing as “the average causal effect of treatment A on outcome Y (period)”,
but “the average causal effect of treatment A on outcome Y in a population
with a particular mix of causal effect modifiers.”
48 Effect modification
Technical Point 4.1
Computing the effect in the treated. We computed the average causal effect in the population under conditional
exchangeability Y
a
⊥⊥A|L for both a = 0 and a = 1. Computing the average causal effect in the treated only requires
partial exchangeability Y
a=0
⊥⊥A|L. In other words, it is irrelevant whether the risk in the untreated, had they been
treated, equals the risk in those who were actually treated. The average causal effect in the untreated is computed
under the partial exchangeability condition Y
a=1
⊥⊥A|L.
We now describe how to compute counterfactual means of the form E [Y
a
|A = a
′
] under the above assumptions of
partial exchangeability. We do so via standardization and via IP weighting:
• Standardization: E[Y
a
|A = a
′
] is equal to
P
l
E [Y |A = a, L = l] Pr [L = l|A = a
′
]. See Miettinen (1972) and
Greenland and Rothman (2008) for a discussion of standardized risk ratios.
• IP weighting: E[Y
a
|A = a
′
] is equal to the IP weighted mean
E
I (A = a) Y
f (A|L)
Pr [A = a
′
|L]
E
I (A = a)
f (A|L)
Pr [A = a
′
|L]
with weights
Pr [A = a
′
|L]
f (A|L)
. For dichotomous A, this equality was derived by Sato and Matsuyama (2003). See Hern´an and
Robins (2006a) for further details.
The extrapolation of causal effects computed in one population to a second
population is referred to as transportability of causal inferences across popula-Some refer to lack of transportabil-
ity as lack of external validity. tions (see Fine Point 4.2). In our example, the causal effect of heart transplant
A on risk of death Y differs between men and women, and between Romans
and Greeks. Thus the average causal effect in this population may not be trans-Hern´an and VanderWeele (2011),
Pearl and Bareinboim (2014), Da-
habreh and Hern´an (2019), and
others have discussed effect mod-
ification in relation to transporting
inferences across populations.
portable to other populations with a different distribution of effect modifiers
such as sex and nationality.
Conditional causal effects in the strata defined by the effect modifiers may
be more transportable than the causal effect in the entire population, but
there is no guarantee that the conditional effect measures in one population
equal the conditional effect measures in another population. This is so be-
cause there could be other unmeasured, or unknown, causal effect modifiers
whose conditional distributions vary between the two populations (or for other
reasons described in Fine Point 4.2). These unmeasured effect modifiers areA setting in which transportabil-
ity may not be an issue: Smith
and Pell (2003) could not identify
any major modifiers of the effect of
parachute use on death after “grav-
itational challenge” (e.g., jumping
from an airplane at high altitude).
They concluded that conducting
randomized trials of parachute use
restricted to a particular group of
people would not compromise the
transportability of the findings to
other groups.
not variables needed to achieve exchangeability, but just risk factors for the
outcome. Therefore, transportability of effects across populations is a more
difficult problem than the identification of causal effects in a single population:
one would need to stratify not just on all those things required to achieve ex-
changeability (which you might have information about, say, by interviewing
those who decide how to allocate the treatment) but on unmeasured causes of
the outcome for which there is much less information.
Hence, transportability of causal effects is an unverifiable assumption that
relies heavily on subject-matter knowledge. For example, most experts would
agree that the health effects (on either the additive or multiplicative scale) of
increasing a household’s annual income by $100 in Niger cannot be transported
to the Netherlands, but most experts would agree that the health effects of use
of cholesterol-lowering drugs in Europeans can be transported to Canadians.
Second, evaluating the presence of effect modification is helpful to identify
4.4 Stratification as a form of adjustment 49
the groups of individuals that would benefit most from an intervention. In
our example of Table 4.1, the average causal effect of treatment A on outcome
Y was null. However, treatment A had a beneficial effect in men (V = 0),
and a harmful effect in women (V = 1). For example, if physicians knew that
there is qualitative effect modification by sex then, in the absence of additional
information, they would treat the next patient only if he happens to be a man.
The situation is slightly more complicated when, as in our second example,
there is multiplicative, but not additive, effect modification. Here treatment
reduces the risk of the outcome by 10% in individuals with V = 0 and also
by 10% in individuals with V = 1, i.e., there is no additive effect modification
by V because the causal risk difference is 0.1 in all levels of V . Thus, an
intervention to treat all patients would be equally effective in reducing risk in
both strata of V , despite the fact that there is multiplicative effect modification.
In fact, if there is a nonzero causal effect in at least one stratum of V and the
counterfactual risk Pr[Y
a=0
= 1|V = v] varies with v, then effect modification
is guaranteed on either the additive or the multiplicative scale.
Additive, but not multiplicative, effect modification is the appropriate scale
to identify the groups that will benefit most from intervention. In the absenceSeveral authors (e.g., Blot and
Day, 1979; Rothman et al., 1980;
Saracci, 1980) have referred to ad-
ditive effect modification as the one
of interest for public health pur-
poses.
of additive effect modification, learning that there is multiplicative effect mod-
ification may not be very helpful for decision making.
In our second example, the presence of multiplicative effect modification
is expected because the risk under no treatment in the stratum V = 1 equals
0.8. Thus, the maximum possible causal risk ratio in the V = 1 stratum is
1/0.8 = 1.25, which is guaranteed to differ from the causal risk ratio of 2 in the
V = 0 stratum. In these situations, multiplicative effect modification arises
from the differences in risk under no treatment Pr[Y
a=0
= 1|V = v] across
levels of V . Therefore, as a general rule, it is more informative to report the
(absolute) counterfactual risks Pr[Y
a=1
= 1|V = v] and Pr[Y
a=0
= 1|V = v]
in every level v of V , rather than simply their ratio or difference.
Finally, the identification of effect modification may help understand the
biological, social, or other mechanisms leading to the outcome. For example, a
greater risk of HIV infection in uncircumcised compared with circumcised men
may provide new clues to understand the disease. The identification of effect
modification may also be a first step towards characterizing the interactions
between two treatments. The terms “effect modification” and “interaction”
are sometimes used as synonymous in the scientific literature. This chapter
focused on “effect modification.” The next chapter describes “interaction” as
a causal concept that is related to, but different from, effect modification.
4.4 Stratification as a form of adjustment
Until this chapter, our only goal was to compute the average causal effect in
the entire population. In the absence of marginal randomization, achieving
this goal requires adjustment for the variables L that ensure conditional ex-
changeability of the treated and the untreated. For example, in Chapter 2 we
determined that the average causal effect of heart transplant A on mortality
Y was null, i.e., the causal risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
= 1. We
used the data in Table 2.2 to adjust for the factor L via both standardization
and IP weighting.
The present chapter adds another potential goal to the analysis: to identify
effect modification by variables V . To achieve this goal, we need to stratify by
50 Effect modification
Fine Point 4.2
Transportability. Effects estimated in one population are often intended to make decisions in another population—the
target population. Can we “transport” the effect from the study population to the target population? The answer
depends on the characteristics of both populations. Specifically, transportability of causal effects across populations
may be justified if the following characteristics are similar between the two populations:
• Effect modification: The causal effect of treatment may differ across individuals with different susceptibility to
the outcome. For example, if women are more susceptible to the effects of treatment than men, we say that sex
is an effect modifier. The distribution of effect modifiers in a population will generally affect the magnitude of the
causal effect of treatment in that population. If the distribution of effect modifiers differs between populations,
then the magnitude of the causal effect of treatment will differ too.
• Versions of treatment: The causal effect of treatment depends on the distribution of versions of treatment in the
population. If this distribution differs between the study population and the target population, then the magnitude
of the causal effect of treatment will differ too (Hern´an and Vanderweele, 2011).
• Interference: In the main text we focus on settings with no interference (Fine Point 1.1). Interference exists when
treating one individual affect the outcome of others in the population. For example, a socially active individual
may convince his friends to join him while exercising, and thus an intervention on that individual’s physical activity
may be more effective than an intervention on a socially isolated individual. Therefore, different contact patterns
between populations will translate into causal effects of different magnitude.
A growing literature considers transportability methods that use data from the study population to estimate the causal
effect in the target population in the presence of effect modification (e.g., Westreich et al. 2017, Rudolph and van der
Laan 2017, Dahabreh et al. 2020b).
The transportability of causal inferences across populations may sometimes be improved by restricting our attention
to the average causal effects in the strata defined by the effect modifiers, or by using the stratum-specific effects in
the study population to reconstruct the average causal effect in the target population. For example, the four stratum-
specific effect measures (Roman women, Greek women, Roman men, and Greek men) in our population can be combined
in a weighted average to reconstruct the average causal effect in another population with a different mix of sex and
nationality. The weight assigned to each stratum-specific measure is the proportion of individuals in that stratum in the
second population. However, there is no guarantee that this reconstructed effect will coincide with the true effect in the
target population because of possible between-population differences in the distribution of unmeasured effect modifiers,
interference patterns, and distribution of versions of treatment.
V in addition to adjusting for L. For example, in this chapter we stratified by
nationality V and adjusted for L to determine that the average causal effect
of heart transplant A on mortality Y differed between Greeks and Romans.
In summary, standardization (or IP weighting) is used to adjust for L and
stratification is used to identify effect modification by V .
But stratification is not always used to identify effect modification by V . In
practice stratification is often used as an alternative to standardization (and
IP weighting) to adjust for L. In fact, the use of stratification as a method
to adjust for L is so widespread that many investigators consider the terms
“stratification” and “adjustment” as synonymous. For example, suppose you
ask an epidemiologist to adjust for the factor L to compute the effect of heart
transplant A on mortality Y . Chances are that she will immediately split
Table 2.2 into two subtables—one restricted to individuals with L = 0, the
other to individuals with L = 1—and would provide the effect measure (say,
the risk ratio) in each of them. That is, she would calculate the risk ratios
4.5 Matching as another form of adjustment 51
Pr [Y = 1|A = 1, L = l] / Pr [Y = 1|A = 0, L = l] = 1 for both l = 0 and l = 1.
These two stratum-specific associational risk ratios can be endowed with a
causal interpretation under conditional exchangeability given L: they measure
the average causal effect in the subsets of the population defined by L = 0
and L = 1, respectively. They are conditional effect measures. In contrast
the risk ratio of 1 that we computed in Chapter 2 was a marginal (uncondi-
tional) effect measure. In this particular example, all three risk ratios—theUnder conditional exchangeability
given L, the risk ratio in the subset
L = l measures the average causal
effect in the subset L = l because,
if Y
a
⊥⊥A|L, then
Pr [Y = 1|A = a, L = 0] =
Pr [Y
a
= 1|L = 0]
two conditional ones and the marginal one—happen to be equal because there
is no effect modification by L. Stratification necessarily results in multiple
stratum-specific effect measures (one per stratum defined by the variables L).
Each of them quantifies the average causal effect in a nonoverlapping subset
of the population but, in general, none of them quantifies the average causal
effect in the entire population. Therefore, we did not consider stratification
when describing methods to compute the average causal effect of treatment in
the population in Chapter 2. Rather, we focused on standardization and IP
weighting.
In addition, unlike standardization and IP weighting, adjustment via strat-
ification requires computing the effect measures in subsets of the population
defined by a combination of all variables L that are required for conditional
exchangeability. For example, when using stratification to estimate the effect
of heart transplant in the population of Tables 2.2 and 4.2, one must compute
the effect in Romans with L = 1, in Greeks with L = 1, in Romans with L = 0,
and in Greeks with L = 0; but one cannot compute the effect in Romans by
simply computing the association in the stratum V = 0 because nationality V ,
by itself, is insufficient to guarantee conditional exchangeability.When considering time-varying
treatments, stratum-specific ef-
fect measures may not have a
causal interpretation even under
exchangeability, positivity, and
well-defined interventions (Robins
1986, 1987). See Chapter 20.
That is, the use of stratification forces one to evaluate effect modification
by all variables L required to achieve conditional exchangeability, regardless of
whether one is interested in such effect modification. In contrast, stratification
by V followed by IP weighting or standardization to adjust for L allows one
to deal with exchangeability and effect modification separately, as described
above.
Other problems associated with the use of stratification are noncollapsi-
bility of certain effect measures like the odds ratio (see Fine Point 4.3) and
inappropriate adjustment that leads to bias when, in the case for time-varying
treatments, it is necessary to adjust for time-varying variables L that are af-Stratification requires positivity in
addition to exchangeability: the
causal effect cannot be computed
in subsets L = l in which there are
only treated, or untreated, individ-
uals.
fected by prior treatment (see Part III).
Sometimes investigators compute the causal effect in only some of the strata
defined by the variables L. That is, no stratum-specific effect measure is com-
puted for some strata. This form of stratification is known as restriction.
For causal inference, stratification is simply the application of restriction to
several comprehensive and mutually exclusive subsets of the population, with
exchangeability within each of these subsets. When positivity fails in some
strata of the population, restriction is used to limit causal inference to those
strata of the original population in which positivity holds (see Chapter 3).
4.5 Matching as another form of adjustment
Matching is another adjustment method. The goal of matching is to construct a
subset of the population in which the variables L have the same distribution in
both the treated and the untreated. As an example, take our heart transplant
example in Table 2.2 in which the variable L is sufficient to achieve conditional
52 Effect modification
exchangeability. For each untreated individual in non critical condition (A =
0, L = 0) randomly select a treated individual in non critical condition (A =
1, L = 0), and for each untreated individual in critical condition (A = 0, L = 1)
randomly select a treated individual in critical condition (A = 1, L = 1). We
refer to each untreated individual and her corresponding treated individual as a
matched pair, and to the variable L as the matching factor. Suppose we formed
the following 7 matched pairs: Rheia-Hestia, Kronos-Poseidon, Demeter-Hera,
Hades-Zeus for L = 0, and Artemis-Ares, Apollo-Aphrodite, Leto-Hermes for
L = 1. All the untreated, but only a sample of treated, in the populationOur discussion on matching applies
to cohort studies only. In case-
control designs (briefly discussed in
Chapter 8), we often match cases
and non-cases (i.e., controls) rather
than the treated and the untreated.
Even if the matching factors suf-
fice for conditional exchangeabil-
ity, matching in cases and controls
does not achieve unconditional ex-
changeability of the treated and the
untreated in the matched popula-
tion. Adjustment for the matching
factors via stratification is required
to estimate conditional (stratum-
specific) effect measures.
were selected. In this subset of the population comprised of matched pairs, the
proportion of individuals in critical condition (L = 1) is the same, by design,
in the treated and in the untreated (3/7).
To construct our matched population we replaced the treated in the pop-
ulation by a subset of the treated in which the matching factor L had the
same distribution as that in the untreated. Under the assumption of condi-
tional exchangeability given L, the result of this procedure is (unconditional)
exchangeability of the treated and the untreated in the matched population.
Because the treated and the untreated are exchangeable in the matched popu-
lation, their average outcomes can be directly compared: the risk in the treated
is 3/7, the risk in the untreated is 3/7, and hence the causal risk ratio is 1. Note
that matching ensures positivity in the matched population because strata with
only treated, or untreated, individuals are excluded from the analysis.
Often one chooses the group with fewer individuals (the untreated in our
example) and uses the other group (the treated in our example) to find their
matches. The chosen group defines the subpopulation on which the causal
effect is being computed. In the previous paragraph we computed the effect in
the untreated. In settings with fewer treated than untreated individuals across
all strata of L, we generally compute the effect in the treated. Also, matching
needs not be one-to-one (matching pairs), but it can be one-to-many (matching
sets).
In many applications, L is a vector of several variables. Then, for each
untreated individual in a given stratum defined by a combination of values of
all the variables in L, we would have randomly selected one (or several) treated
individual(s) from the same stratum.
Matching can be used to create a matched population with any chosenAs the number of matching fac-
tors increases, so does the proba-
bility that no exact matches exist
for an individual. There is a vast
literature, beyond the scope of this
book, on how to find approximate
matches in those settings. See Stu-
art (2010) for an introduction.
distribution of L, not just the distribution in the treated or the untreated. The
distribution of interest can be achieved by individual matching, as described
above, or by frequency matching. An example of the latter is a study in which
one randomly selects treated individuals in such a way that 70% of them have
L = 1, and then repeats the same procedure for the untreated.
Because the matched population is a subset of the original study population,
the distribution of causal effect modifiers in the matched study population
will generally differ from that in the original, unmatched study population, as
discussed in the next section.
4.6 Effect modification and adjustment methods
Standardization, IP weighting, stratification/restriction, and matching are dif-
ferent approaches to estimate average causal effects, but they estimate different
types of causal effects. These four approaches can be divided into two groups
according to the type of effect they estimate: standardization and IP weight-
4.6 Effect modification and adjustment methods 53
Technical Point 4.2
Pooling of stratum-specific effect measures. Until Chapter 10, we avoid statistical considerations by assuming that
we work with the entire population rather than with a sample. Thus we talk about computing causal effects rather than
about (consistently) estimating them. In practice, however, we can rarely compute causal effects in the population. We
estimate them from samples and wish to obtaining reasonably narrow confidence intervals around our effect estimates.
When dealing with stratum-specific effect measures, a common approach to reduce the variability of the estimates
is to combine all stratum-specific effect measures into one pooled stratum-specific effect measure. The idea is that, if
there is no effect-measure modification, the pooled effect measure will be a more precise estimate of the common effect
measure than each of the stratum-specific effect measures. Pooling methods (e.g., Woolf, Mantel-Haenszel, maximum
likelihood) sometimes compute a weighted average of the stratum-specific effect measures with weights chosen to reduce
the variability of the pooled estimate. Greenland and Rothman (2008) review some commonly used methods for stratified
analysis. Pooled effect measures can also be computed using regression models that include all possible product terms
between all covariates L, but no product terms between treatment A and covariates L, i.e., models saturated (see
Chapter 11) with respect to L.
The main goal of pooling is to obtain a narrower confidence interval around the common stratum-specific effect
measure, but the pooled effect measure is still a conditional effect measure. In our heart transplant example, the pooled
stratum-specific risk ratio (Mantel-Haenszel method) was 0.88 for the outcome Z. This result is only meaningful if
the stratum-specific risk ratios 2 and 0.5 are indeed estimates of the same stratum-specific causal effect. For example,
suppose that the causal risk ratio is 0.9 in both strata but, because of the small sample size, we obtained estimates of
0.5 and 2.0. In that case, pooling would be appropriate and the Mantel-Haenszel risk ratio would be closer to the truth
than either of the stratum-specific risk ratios. Otherwise, if the causal stratum-specific risk ratios are truly 0.5 and 2.0,
then pooling makes little sense and the Mantel-Haenszel risk ratio could not be easily interpreted. The same issues arise
in meta-analyses of studies with heterogeneous treatment effects (Dahabreh et al. 2020a).
In practice, it is not always obvious to determine whether the heterogeneity of the effect measure across strata is
due to sampling variability or to effect-measure modification. The finer the stratification, the greater the uncertainty
introduced by random variability.
ing can be used to compute either marginal or conditional effects, stratifica-Table 4.3
L A Z
Rheia 0 0 0
Kronos 0 0 1
Demeter 0 0 0
Hades 0 0 0
Hestia 0 1 0
Poseidon 0 1 0
Hera 0 1 1
Zeus 0 1 1
Artemis 1 0 1
Apollo 1 0 1
Leto 1 0 0
Ares 1 1 1
Athena 1 1 1
Hephaestus 1 1 1
Aphrodite 1 1 0
Polyphemus 1 1 0
Persephone 1 1 0
Hermes 1 1 0
Hebe 1 1 0
Dionysus 1 1 0
tion/restriction and matching can only be used to compute conditional effects
in certain subsets of the population. All four approaches require exchangeabil-
ity and positivity but the subsets of the population in which these conditions
need to hold depend on the causal effect of interest. For example, to compute
the conditional effect among individuals with L = l, any of the above meth-
ods requires exchangeability and positivity in that subset only; to estimate
the marginal effect in the entire population, exchangeability and positivity are
required in all levels of L.
In the absence of effect modification, the effect measures (risk ratio or risk
difference) computed via these four approaches will be equal. For example,
we concluded that the average causal effect of heart transplant A on mortality
Y was null both in the entire population of Table 2.2 (standardization and IP
weighting), in the subsets of the population in critical condition L = 1 and non
critical condition L = 0 (stratification), and in the untreated (matching). All
methods resulted in a causal risk ratio equal to 1. However, the effect measures
computed via these four approaches will not generally be equal. To illustrate
how the effects may vary, let us compute the effect of heart transplant A on
high blood pressure Z (1: yes, 0 otherwise) using the data in Table 4.3. We
assume that exchangeability Z
a
⊥⊥A|L and positivity hold. We use the risk
ratio scale for no particular reason.
Standardization and IP weighting yield the average causal effect in the
54 Effect modification
Technical Point 4.3
Relation between marginal and conditional causal risk ratios. Suppose we wish to determine under which
conditions the marginal risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
will be less than 1 given that we know the
values of the conditional risk ratios Pr
Y
a=1
= 1|L = l
/ Pr
Y
a=0
= 1|L = l
for each stratum l. To do so,
note that Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
=
P
l
Pr
Y
a=1
= 1|L = l
/ Pr
Y
a=0
= 1|L = l
w (l), with w (l) =
Pr
Y
a=0
= 1|L = l
Pr [L = l]
/ Pr
Y
a=0
= 1
and
P
l
w (l) = 1. Substituting for w (1) and w (0) followed by
some algebraic manipulations will provide the condition under which the inequality Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
< 1
holds.
In our data example, Pr
Y
a=1
= 1|L = l
/ Pr
Y
a=0
= 1|L = l
is 0.5 for L = 1 and 2.0 for L = 0. There-
fore the marginal risk ratio will be less than 1 if and only if Pr
Y
a=0
= 1|L = 1
/ Pr
Y
a=0
= 1|L = 0
>
2 Pr [L = 0] / Pr [L = 1].
entire population Pr[Z
a=1
= 1]/ Pr[Z
a=0
= 1] = 0.8 (these and the following
calculations are left to the reader). Stratification yields the conditional causalTable 4.4
V A Y
Rheia 1 0 0
Demeter 1 0 0
Hestia 1 0 0
Hera 1 0 0
Artemis 1 0 1
Leto 1 1 0
Athena 1 1 1
Aphrodite 1 1 1
Persephone 1 1 0
Hebe 1 1 1
Kronos 0 0 0
Hades 0 0 0
Poseidon 0 0 1
Zeus 0 0 1
Apollo 0 0 0
Ares 0 1 1
Hephaestus 0 1 1
Polyphemus 0 1 1
Hermes 0 1 0
Dionysus 0 1 1
risk ratios Pr[Z
a=1
= 1|L = 0]/ Pr[Z
a=0
= 1|L = 0] = 2.0 in the stratum L =
0, and Pr[Z
a=1
= 1|L = 1]/ Pr[Z
a=0
= 1|L = 1] = 0.5 in the stratum L = 1.
Matching, using the matched pairs selected in the previous section, yields the
causal risk ratio in the untreated Pr[Z
a=1
= 1|A = 0]/ Pr[Z = 1|A = 0] = 1.0.
We have computed four causal risk ratios and have obtained four different
numbers: 0.8, 2.0, 0.5, and 1.0. All of them are correct. Leaving aside random
variability (see Technical Point 4.2), the explanation of the differences is qual-
itative effect modification: Treatment doubles the risk among individuals in
noncritical condition (L = 0, causal risk ratio 2.0) and halves the risk among
individuals in critical condition (L = 1, causal risk ratio 0.5). The average
causal effect in the population (causal risk ratio 0.8) is beneficial because the
ratio Pr
Z
a=0
= 1|L = 1
/ Pr
Z
a=0
= 1|L = 0
of the counterfactual risk un-
der no treatment in the critical group to that in the noncritical group exceeds
2 times the odds Pr [L = 0] / Pr [L = 1] of being in the noncritical group (see
Technical Point 4.3). The causal effect in the untreated is null (causal risk ratio
1.0), which reflects the larger proportion of individuals in noncritical condition
in the untreated compared with the entire population. This example high-
lights the primary importance of specifying the population, or the subset of a
population, to which the effect measure corresponds.
The previous chapter argued that a well-defined causal effect is a prereq-
uisite for meaningful causal inference. This chapter argues that a well charac-
terized target population is another such prerequisite. Both prerequisites are
automatically present in experiments that compare two or more interventions
in a population that meets certain a priori eligibility criteria. However, thesePart II describes how standardiza-
tion, IP weighting, and stratifica-
tion can be used in combination
with parametric or semiparametric
models. For example, standard re-
gression models are a form of strati-
fication in which the association be-
tween treatment and outcome is es-
timated within levels of all the other
covariates in the model.
prerequisites cannot be taken for granted in observational studies. Rather, in-
vestigators conducting observational studies need to explicitly define the causal
effect of interest and the subset of the population in which the effect is being
computed. Otherwise, misunderstandings might easily arise when effect mea-
sures obtained via different methods are different.
In our example above, one investigator who used IP weighting (and com-
puted the effect in the entire population) and another one who used matching
(and computed the effect in the untreated) need not engage in a debate about
the superiority of one analytic approach over the other. Their discrepant effect
measures result from the different causal question asked by each investigator
rather than from their choice of analytic approach. In fact, the second investi-
4.6 Effect modification and adjustment methods 55
gator could have used IP weighting to compute the effect in the untreated or
in the treated (see Technical Point 4.1).
A final note. Stratification can be used to compute average causal effects
in subsets of the population, but not individual (subject-specific) effects. As
we have discussed earlier, individual causal effects can only be identified under
extreme assumptions. See Fine Points 2.1 and 3.2.
56 Effect modification
Fine Point 4.3
Collapsibility and the odds ratio. In the absence of multiplicative effect modification by V , the causal risk ratio in
the entire population, Pr[Y
a=1
= 1]/ Pr[Y
a=0
= 1] is equal to the conditional causal risk ratios Pr[Y
a=1
= 1|V =
v]/ Pr[Y
a=0
= 1|V = v] in every stratum v of V . More generally, the causal risk ratio is a weighted average of the
stratum-specific risk ratios. For example, if the causal risk ratios in the strata V = 1 and V = 0 were equal to 2 and 3,
respectively, then the causal risk ratio in the population would be greater than 2 and less than 3. That the value of the
causal risk ratio (and the causal risk difference) in the population is always constrained by the range of values of the
stratum-specific risk ratios is not only obvious but also a desirable characteristic of any effect measure.
Now consider a hypothetical effect measure (other than the risk ratio or the risk difference) such that the population
effect measure were not a weighted average of the stratum-specific measures. That is, the population effect measure
would not necessarily lie inside of the range of values of the stratum-specific effect measures. Such effect measure would
be an odd one. The odds ratio (pun intended) is such an effect measure, as we now discuss.
Suppose the data in Table 4.4 were collected to compute the causal effect of altitude A on depression Y in a population
of 20 individuals who were not depressed at baseline. The treatment A is 1 if the individual moved to a high altitude
residence (on the top of Mount Olympus), 0 otherwise; the outcome Y is 1 if the individual subsequently developed
depression, 0 otherwise; and V is 1 if the individual was a woman, 0 if a man. The decision to move was random,
i.e., those more prone to develop depression were as likely to move as the others; effectively Y
a
⊥⊥A. Therefore the
risk ratio Pr[Y = 1|A = 1]/ Pr[Y = 1|A = 0] = 2.3 is the causal risk ratio in the population, and the odds ratio
Pr[Y = 1|A = 1]/ Pr[Y = 0|A = 1]
Pr[Y = 1|A = 0]/ Pr[Y = 0|A = 0]
= 5.4 is the causal odds ratio
Pr[Y
a=1
= 1]/ Pr[Y
a=1
= 0]
Pr[Y
a=0
= 1]/ Pr[Y
a=0
= 0]
in the population.
The risk ratio and the odds ratio measure the same causal effect on different scales.
Let us now compute the sex-specific causal effects on the risk ratio and odds ratio scales. The (conditional) causal
risk ratio Pr[Y = 1|V = v, A = 1]/ Pr[Y = 1|V = v, A = 0] is 2 for men (V = 0) and 3 for women (V = 1).
The (conditional) causal odds ratio
Pr[Y = 1|V = v, A = 1]/ Pr[Y = 0|V = v, A = 1]
Pr[Y = 1|V = v, A = 0]/ Pr[Y = 0|V = v, A = 0]
is 6 for men (V = 0) and 6 for
women (V = 1). The causal risk ratio in the population, 2.3, is in between the sex-specific causal risk ratios 2 and 3. In
contrast, the causal odds ratio in the population, 5.4, is smaller (i.e., closer to the null value) than both sex-specific odds
ratios, 6. The causal effect, when measured on the odds ratio scale, is bigger in each half of the population than in the
entire population. The population causal odds ratio can be closer to the null value than the non-null stratum-specific
causal odds ratio when V is an independent risk factor for Y and, as in our randomized experiment, A is independent
of V (Miettinen and Cook, 1981).
We say that an effect measure is collapsible when the population effect measure can be expressed as a weighted
average of the stratum-specific measures. In follow-up studies the risk ratio and the risk difference are collapsible effect
measures, but the odds ratio—or the rarely used odds difference—is not (Greenland 1987). The noncollapsibility of the
odds ratio, which is a special case of Jensen’s inequality (Samuels 1981), may lead to counterintuitive findings like those
described above. The odds ratio is collapsible under the sharp null hypothesis—both the conditional and unconditional
effect measures are then equal to the null value—and it is approximately collapsible—and approximately equal to the
risk ratio—when the outcome is rare (say, < 10%) in every stratum of a follow-up study.
One important consequence of the noncollapsibility of the odds ratio is the logical impossibility of equating “lack of
exchangeability” and “change in the conditional odds ratio compared with the unconditional odds ratio.” In our example,
the change in odds ratio was about 10% (1 − 6/5.4) even though the treated and the untreated were exchangeable.
Greenland, Robins, and Pearl (1999) reviewed the relation between noncollapsibility and lack of exchangeability.
Chapter 5
INTERACTION
Consider again a randomized experiment to answer the causal question “does one’s looking up at the sky make
other pedestrians look up too?” We have so far restricted our interest to the causal effect of a single treatment
(looking up) in either the entire population or a subset of it. However, many causal questions are actually about
the effects of two or more simultaneous treatments. For example, suppose that, besides randomly assigning your
looking up, we also randomly assign whether you stand in the street dressed or naked. We can now ask questions
like: what is the causal effect of your looking up if you are dressed? And if you are naked? If these two causal
effects differ we say that the two treatments under consideration (looking up and being dressed) interact in bringing
about the outcome.
When joint interventions on two or more treatments are feasible, the identification of interaction allows one
to implement the most effective interventions. Thus understanding the concept of interaction is key for causal
inference. This chapter provides a formal definition of interaction between two treatments, both within our already
familiar counterfactual framework and within the sufficient-component-cause framework.
5.1 Interaction requires a joint intervention
Suppose that in our heart transplant example, individuals were assigned to
receiving either a multivitamin complex (E = 1) or no vitamins (E = 0)
before being assigned to either heart transplant (A = 1) or no heart trans-
plant (A = 0). We can now classify all individuals into 4 treatment groups:
vitamins-transplant (E = 1, A = 1), vitamins-no transplant (E = 1, A = 0),
no vitamins-transplant (E = 0, A = 1), and no vitamins-no transplant (E = 0,
A = 0). For each individual, we can now imagine 4 potential or counterfac-
tual outcomes, one under each of these 4 treatment combinations: Y
a=1,e=1
,
Y
a=1,e=0
, Y
a=0,e=1
, and Y
a=0,e=0
. In general, an individual’s counterfactual
outcome Y
a,e
is the outcome that would have been observed if we had inter-
vened to set the individual’s values of A and E to a and e, respectively. We
refer to interventions on two or more treatments as joint interventions.The counterfactual Y
a
correspond-
ing to an intervention on A alone
is the joint counterfactual Y
a,e
if
the observed E takes the value e,
i.e., Y
a
= Y
a,E
. In fact, consis-
tency is a special case of this recur-
sive substitution. Specifically, the
observed Y = Y
A
= Y
A,E
, which
is our definition of consistency. See
also Technical Point 6.2.
We are now ready to provide a definition of interaction within the coun-
terfactual framework. There is interaction between two treatments A and E
if the causal effect of A on Y after a joint intervention that set E to 1 differs
from the causal effect of A on Y after a joint intervention that set E to 0. For
example, there would be an interaction between transplant A and vitamins
E if the causal effect of transplant on survival had everybody taken vitamins
were different from the causal effect of transplant on survival had nobody taken
vitamins.
When the causal effect is measured on the risk difference scale, we say that
there is interaction betweenA and E on the additive scale in the population if
Pr
Y
a=1,e=1
= 1
−Pr
Y
a=0,e=1
= 1
= Pr
Y
a=1,e=0
= 1
−Pr
Y
a=0,e=0
= 1
.
For example, suppose the causal risk difference for transplant A when ev-
erybody receives vitamins, Pr
Y
a=1,e=1
= 1
− Pr
Y
a=0,e=1
= 1
, were 0.1,
58 Interaction
and that the causal risk difference for transplant A when nobody receives vi-
tamins, Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
, were 0.2. We say that there
is interaction between A and E on the additive scale because the risk dif-
ference Pr
Y
a=1,e=1
= 1
− Pr
Y
a=0,e=1
= 1
is less than the risk difference
Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
. Using simple algebra, it can be easily
shown that this inequality implies that the causal risk difference for vitamins E
when everybody receives a transplant, Pr
Y
a=1,e=1
= 1
−Pr
Y
a=1,e=0
= 1
,
is also less than the causal risk difference for vitamins E when nobody re-
ceives a transplant A, Pr
Y
a=0,e=1
= 1
−Pr
Y
a=0,e=0
= 1
. That is, we can
equivalently define interaction between A and E on the additive scale as
Pr
Y
a=1,e=1
= 1
−Pr
Y
a=1,e=0
= 1
= Pr
Y
a=0,e=1
= 1
−Pr
Y
a=0,e=0
= 1
.
The two inequalities displayed above show that treatments A and E have equal
status in the definition of interaction.
Let us now review the difference between interaction and effect modifica-
tion. As described in the previous chapter, a variable V is a modifier of the
effect of A on Y when the average causal effect of A on Y varies across levels of
V . Note the concept of effect modification refers to the causal effect of A, not
to the causal effect of V . For example, sex was an effect modifier for the effect
of heart transplant in Table 4.1, but we never discussed the effect of sex on
death. Thus, when we say that V modifies the effect of A we are not consid-
ering V and A as variables of equal status, because only A is considered to be
a variable on which we could hypothetically intervene. That is, the definition
of effect modification involves the counterfactual outcomes Y
a
, not the coun-
terfactual outcomes Y
a,v
. In contrast, the definition of interaction between A
and E gives equal status to both treatments A and E, as reflected by the two
equivalent definitions of interaction shown above. The concept of interaction
refers to the joint causal effect of two treatments A and E, and thus involves
the counterfactual outcomes Y
a,e
under a joint intervention.
5.2 Identifying interaction
In previous chapters we have described the conditions that are required to
identify the average causal effect of a treatment A on an outcome Y , either
in the entire population or in a subset of it. The three key identifying condi-
tions were exchangeability, positivity, and consistency. Because interaction is
concerned with the joint effect of two (or more) treatments A and E, identi-
fying interaction requires exchangeability, positivity, and consistency for both
treatments.
Suppose that vitamins E were randomly, and unconditionally, assigned by
the investigators. Then positivity and consistency hold, and the treated E = 1
and the untreated E = 0 are expected to be exchangeable. That is, the risk
that would have been observed if all individuals had been assigned to transplant
A = 1 and vitamins E = 1 equals the risk that would have been observed if
all individuals who received E = 1 had been assigned to transplant A = 1.
Formally, the marginal risk Pr
Y
a=1,e=1
= 1
is equal to the conditional risk
Pr
Y
a=1
= 1|E = 1
. As a result, we can rewrite the definition of interaction
between A and E on the additive scale as
Pr
Y
a=1
= 1|E = 1
− Pr
Y
a=0
= 1|E = 1
= Pr
Y
a=1
= 1|E = 0
− Pr
Y
a=0
= 1|E = 0
,
5.2 Identifying interaction 59
Technical Point 5.1
Interaction on the additive and multiplicative scales. The equality of causal risk differences Pr
Y
a=1,e=1
= 1
−
Pr
Y
a=0,e=1
= 1
= Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
can be rewritten as
Pr
Y
a=1,e=1
= 1
=
Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
+ Pr
Y
a=0,e=1
= 1
.
By subtracting Pr
Y
a=0,e=0
= 1
from both sides of the equation, we get Pr
Y
a=1,e=1
= 1
− Pr
Y
a=0,e=0
= 1
=
Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
+
Pr
Y
a=0,e=1
= 1
− Pr
Y
a=0,e=0
= 1
.
This equality is another compact way to show that treatments A and E have equal status in the definition of interaction.
When the above equality holds, we say that there is no interaction between A and E on the additive scale, and we
say that the causal risk difference Pr
Y
a=1,e=1
= 1
− Pr
Y
a=0,e=0
= 1
is additive because it can be written as the
sum of the causal risk differences that measure the effect of A in the absence of E and the effect of E in the absence of
A. Conversely, there is interaction between A and E on the additive scale if Pr
Y
a=1,e=1
= 1
−Pr
Y
a=0,e=0
= 1
=
Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
+
Pr
Y
a=0,e=1
= 1
− Pr
Y
a=0,e=0
= 1
.
The interaction is superadditive if the ‘not equal to’ (=) symbol can be replaced by a ‘greater than’ (>) symbol. The
interaction is subadditive if the ‘not equal to’ (=) symbol can be replaced by a ‘less than’ (<) symbol.
Analogously, one can define interaction on the multiplicative scale when the effect measure is the causal risk ratio,
rather than the causal risk difference. We say that there is interaction between A and E on the multiplicative scale if
Pr
Y
a=1,e=1
= 1
Pr [Y
a=0,e=0
= 1]
=
Pr
Y
a=1,e=0
= 1
Pr [Y
a=0,e=0
= 1]
×
Pr
Y
a=0,e=1
= 1
Pr [Y
a=0,e=0
= 1]
.
The interaction is supermultiplicative if the ‘not equal to’ (=) symbol can be replaced by a ‘greater than’ (>) symbol.
The interaction is submultiplicative if the ‘not equal to’ (=) symbol can be replaced by a ‘less than’ (<) symbol.
which is exactly the definition of modification of the effect of A by E on the
additive scale. In other words, when treatment E is randomly assigned, then
the concepts of interaction and effect modification coincide. The methods
described in Chapter 4 to identify modification of the effect of A by V can now
be applied to identify interaction of A and E by simply replacing the effect
modifier V by the treatment E.
Now suppose treatment E was not assigned by investigators. To assess the
presence of interaction between A and E, one still needs to compute the four
marginal risks Pr [Y
a,e
= 1]. In the absence of marginal randomization, these
risks can be computed for both treatments A and E, under the usual identifying
assumptions, by standardization or IP weighting conditional on the measured
covariates. An equivalent way of conceptualizing this problem follows: rather
than viewing A and E as two distinct treatments with two possible levels (1
or 0) each, one can view AE as a combined treatment with four possible levels
(11, 01, 10, 00). Under this conceptualization the identification of interaction
between two treatments is not different from the identification of the causal
effect of one treatment that we have discussed in previous chapters. The same
methods, under the same identifiability conditions, can be used. The only
difference is that now there is a longer list of values that the treatment of
interest can take, and therefore a greater number of counterfactual outcomes.
Sometimes one may be willing to assume (conditional) exchangeability for
60 Interaction
treatment A but not for treatment E, e.g., when estimating the causal effect
of A in subgroups defined by E in a randomized experiment. In that case, one
cannot generally assess the presence of interaction between A and E, but can
still assess the presence of effect modification by E. This is so because one
does not need any identifying assumptions involving E to compute the effect
of A in each of the strata defined by E. In the previous chapter we used the
notation V (rather than E) for variables for which we are not willing to make
assumptions about exchangeability, positivity, and consistency. For example,
we concluded that the effect of transplant A was modified by nationality V ,
but we never required any identifying assumptions for the effect of V because
we were not interested in using our data to compute the causal effect of V
on Y . In Section 4.2 we argued on substantive grounds that V is a surrogate
effect modifier; that is, V does not act on the outcome and therefore does not
interact with A—no action, no interaction. But V is a modifier of the effect
of A on Y because V is correlated with (e.g., it is a proxy for) an unidentified
variable that actually has an effect on Y and interacts with A. Thus thereInteraction between A and E with-
out modification of the effect of
A by E is also logically possible,
though probably rare, because it
requires dual effects of A and
exact cancellations (VanderWeele
2009b).
can be modification of the effect of A by another variable without interaction
between A and that variable.
In the above paragraphs we have argued that a sufficient condition for
identifying interaction between two treatments A and E is that exchangeability,
positivity, and consistency are all satisfied for the joint treatment (A, E) with
the four possible values (0, 0), (0, 1), (1, 0), and (1, 1). Then standardization
or IP weighting can be used to estimate the joint effects of the two treatments
and thus to evaluate interaction between them. In Part III, we show that this
condition is not necessary when the two treatments occur at different times.
For the remainder of Part I (except this chapter) and most of Part II, we will
focus on the causal effect of a single treatment A.
In Chapter 1 we described deterministic and nondeterministic counterfac-
tual outcomes. Up to here, we used deterministic counterfactuals for simplicity.
However, none of the results we have discussed for population causal effects
and interactions require deterministic counterfactual outcomes. In contrast,
the following section of this chapter only applies in the case that counterfactu-
als are deterministic. Further, we also assume that treatments and outcomes
are dichotomous.
5.3 Counterfactual response types and interaction
Individuals can be classified in terms of their deterministic counterfactual re-
sponses. For example, in Table 4.1 (same as Table 1.1), there are four types
of people: the “doomed” who will develop the outcome regardless of what
treatment they receive (Artemis, Athena, Persephone, Ares), the “immune”
who will not develop the outcome regardless of what treatment they receive
(Demeter, Hestia, Hera, Hades), the “helped” who will develop the outcome
only if untreated (Hebe, Kronos, Poseidon, Apollo, Hermes, Dyonisus), and theTable 5.1
Type Y
a=0
Y
a=1
Doomed 1 1
Helped 1 0
Hurt 0 1
Immune 0 0
“hurt” who will develop the outcome only if treated (Rheia, Leto, Aphrodite,
Zeus, Hephaestus, Polyphemus). Each combination of counterfactual responses
is often referred to as a response pattern or a response type. Table 5.1 display
the four possible response types.
When considering two dichotomous treatments A and E, there are 16 pos-
sible response types because each individual has four counterfactual outcomes,
one under each of the four possible joint interventions on treatments A and
5.3 Counterfactual response types and interaction 61
E: (1, 1), (0, 1), (1, 0), and (0, 0). Table 5.2 shows the 16 response types for
two treatments. This section explores the relation between response types and
the presence of interaction in the case of two dichotomous treatments A and
E and a dichotomous outcome Y .
The first type in Table 5.2 has the counterfactual outcome Y
a=1,e=1
equal
to 1, which means that an individual of this type would die if treated with
both transplant and vitamins. The other three counterfactual outcomes are
also equal to 1, i.e., Y
a=1,e=1
= Y
a=0,e=1
= Y
a=1,e=0
= Y
a=0,e=0
= 1, which
means that an individual of this type would also die if treated with (no trans-Table 5.2
Y
a,e
for each a, e value
Type 1, 1 0, 1 1, 0 0, 0
1 1 1 1 1
2 1 1 1 0
3 1 1 0 1
4 1 1 0 0
5 1 0 1 1
6 1 0 1 0
7 1 0 0 1
8 1 0 0 0
9 0 1 1 1
10 0 1 1 0
11 0 1 0 1
12 0 1 0 0
13 0 0 1 1
14 0 0 1 0
15 0 0 0 1
16 0 0 0 0
plant, vitamins), (transplant, no vitamins), or (no transplant, no vitamins).
In other words, neither treatment A nor treatment E has any effect on the
outcome of such individual. He would die no matter what joint treatment he
is assigned to. Now consider type 16. All the counterfactual outcomes are 0,
i.e., Y
a=1,e=1
= Y
a=0,e=1
= Y
a=1,e=0
= Y
a=0,e=0
= 0. Again, neither treat-
ment A nor treatment E has any effect on the outcome of an individual of this
type. She would survive no matter what joint treatment she is assigned to.
If all individuals in the population were of types 1 and 16, we would say that
neither A nor E has any causal effect on Y ; the sharp causal null hypothesis
would be true for the joint treatment (A, E).
Let us now focus our attention on types 4, 6, 11, and 13. Individuals of type
4 would only die if treated with vitamins, whether they do or do not receive
a transplant, i.e., Y
a=1,e=1
= Y
a=0,e=1
= 1 and Y
a=1,e=0
= Y
a=0,e=0
= 0.
Individuals of type 13 would only die if not treated with vitamins, whether
they do or do not receive a transplant, i.e., Y
a=1,e=1
= Y
a=0,e=1
= 0 and
Y
a=1,e=0
= Y
a=0,e=0
= 1. Individuals of type 6 would only die if treated
with transplant, whether they do or do not receive vitamins, i.e., Y
a=1,e=1
=
Y
a=1,e=0
= 1 and Y
a=0,e=1
= Y
a=0,e=0
= 0. Individuals of type 11 would only
die if not treated with transplant, whether they do or do not receive vitamins,
i.e., Y
a=1,e=1
= Y
a=1,e=0
= 0 and Y
a=0,e=1
= Y
a=0,e=0
= 1.Miettinen (1982) described the 16
possible response types under two
binary treatments and outcome.
Of the 16 possible response types in Table 5.2, we have identified 6 types
(numbers 1, 4, 6, 11, 13, 16) with a common characteristic: for an individual
with one of those response types, the causal effect of treatment A on the out-
come Y is the same regardless of the value of treatment E, and the causal effect
of treatment E on the outcome Y is the same regardless of the value of treat-
ment A. In a population in which every individual has one of these 6 response
types, the causal effect of treatment A in the presence of treatment E, as
measured by the causal risk difference Pr
Y
a=1,e=1
= 1
−Pr
Y
a=0,e=1
= 1
,
would equal the causal effect of treatment A in the absence of treatment E, as
measured by the causal risk difference Pr
Y
a=1,e=0
= 1
−Pr
Y
a=0,e=0
= 1
.
That is, if all individuals in the population have response types 1, 4, 6, 11,
13 and 16 then there will be no interaction between A and E on the additive
scale.
The presence of additive interaction between A and E implies that, for someGreenland and Poole (1988) noted
that Miettinen’s response types
were not invariant to recoding of
A and E (i.e., switching the labels
“0” and “1 ”). They partitioned
the 16 response types of Table 5.2
into these three equivalence classes
that are invariant to recoding.
individuals in the population, the value of their two counterfactual outcomes
under A = a cannot be determined without knowledge of the value of E, and
vice versa. That is, there must be individuals in at least one of the following
three classes:
1. those who would develop the outcome under only one of the four treat-
ment combinations (types 8, 12, 14, and 15 in Table 5.2)
2. those who would develop the outcome under two treatment combinations,
with the particularity that the effect of each treatment is exactly the
opposite under each level of the other treatment (types 7 and 10)
62 Interaction
Technical Point 5.2
Monotonicity of causal effects. Consider a setting with a dichotomous treatment A and outcome Y . The value
of the counterfactual outcome Y
a=0
is greater than that of Y
a=1
only among individuals of the “helped” type. For
the other 3 types, Y
a=1
≥ Y
a=0
or, equivalently, an individual’s counterfactual outcomes are monotonically increasing
(i.e., nondecreasing) in a. Thus, when the treatment cannot prevent any individual’s outcome (i.e., in the absence of
“helped” individuals), all individuals’ counterfactual response types are monotonically increasing in a. We then simply
say that the causal effect of A on Y is monotonic.
The concept of monotonicity can be generalized to two treatments A and E. The causal effects of A and E on
Y are monotonic if every individual’s counterfactual outcomes Y
a,e
are monotonically increasing in both a and e.
That is, if there are no individuals with response types
Y
a=1,e=1
= 0, Y
a=0,e=1
= 1
,
Y
a=1,e=1
= 0, Y
a=1,e=0
= 1
,
Y
a=1,e=0
= 0, Y
a=0,e=0
= 1
, and
Y
a=0,e=1
= 0, Y
a=0,e=0
= 1
.
3. those who would develop the outcome under three of the four treatment
combinations (types 2, 3, 5, and 9)
On the other hand, the absence of additive interaction between A and
E implies that either no individual in the population belongs to one of the
three classes described above, or that there is a perfect cancellation of equalFor more on cancellations that re-
sult in additivity even when inter-
action types are present, see Green-
land, Lash, and Rothman (2008).
deviations from additivity of opposite sign. Such cancellation would occur,
e.g., if there were an equal proportion of individuals of types 7 and 10, or of
types 8 and 12.
The meaning of the term “interaction” is clarified by the classification of
individuals according to their counterfactual response types (see also Fine Point
5.1). We now introduce a tool to conceptualize the causal mechanisms involved
in the interaction between two treatments.
5.4 Sufficient causes
The meaning of interaction is clarified by the classification of individuals ac-
cording to their counterfactual response types. We now introduce a tool to
represent the causal mechanisms involved in the interaction between two treat-
ments. Consider again our heart transplant example with a single treatment
A. As reviewed in the previous section, some individuals die when they are
treated, others when they are not treated, others die no matter what, and
others do not die no matter what. This variety of response types indicates
that treatment A is not the only variable that determines whether or not the
outcome Y occurs.
Take those individuals who were actually treated. Only some of them died,
which implies that treatment alone is insufficient to always bring about the
outcome. As an oversimplified example, suppose that heart transplant A = 1
only results in death in individuals allergic to anesthesia. We refer to the
smallest set of background factors that, together with A = 1, are sufficient to
inevitably produce the outcome as U
1
. The simultaneous presence of treatment
(A = 1) and allergy to anesthesia (U
1
= 1) is a minimal sufficient cause of the
outcome Y .
Now take those individuals who were not treated. Again only some of them
died, which implies that lack of treatment alone is insufficient to bring about
the outcome. As an oversimplified example, suppose that no heart transplant
5.4 Sufficient causes 63
Fine Point 5.1
More on counterfactual types and interaction. The classification of individuals by counterfactual response types
makes it easier to consider specific forms of interaction. For example, we may be interested in learning whether some
individuals will develop the outcome when receiving both treatments E = 1 and A = 1, but not when receiving only one
of the two. That is, whether individuals with counterfactual responses Y
a=1,e=1
= 1 and Y
a=0,e=1
= Y
a=1,e=0
= 0
(types 7 and 8) exist in the population. VanderWeele and Robins (2007a, 2008) developed a theory of sufficient cause
interaction for 2 and 3 treatments, and derived the identifying conditions for synergism that are described here. The
following inequality is a sufficient condition for these individuals to exist:
Pr
Y
a=1,e=1
= 1
−
Pr
Y
a=0,e=1
= 1
+ Pr
Y
a=1,e=0
= 1
> 0
or, equivalently, Pr
Y
a=1,e=1
= 1
− Pr
Y
a=0,e=1
= 1
> Pr
Y
a=1,e=0
= 1
That is, in an experiment in which treatments A and E are randomly assigned, one can compute the three counterfactual
risks in the above inequality, and empirically check that individuals of types 7 and 8 exist.
Because the above inequality is a sufficient but not a necessary condition, it may not hold even if types 7 and 8 exist.
In fact this sufficient condition is so strong that it may miss most cases in which these types exist. A weaker sufficient
condition for synergism can be used if one knows, or is willing to assume, that receiving treatments A and E cannot
prevent any individual from developing the outcome, i.e., if the effects are monotonic (see Technical Point 5.2). In this
case, the inequality
Pr
Y
a=1,e=1
= 1
− Pr
Y
a=0,e=1
= 1
> Pr
Y
a=1,e=0
= 1
− Pr
Y
a=0,e=0
= 1
is a sufficient condition for the existence of types 7 and 8. In other words, when the effects of A and E are monotonic,
the presence of superadditive interaction implies the presence of type 8 (monotonicity rules out type 7). This sufficient
condition for synergism under monotonic effects was originally reported by Greenland and Rothman in a previous edition
of their book. It is now reported in Greenland, Lash, and Rothman (2008).
In genetic research it is sometimes interesting to determine whether there are individuals of type 8, a form of interaction
referred to as compositional epistasis. VanderWeele (2010a) reviews empirical tests for compositional epistasis.
A = 0 only results in death if individuals have an ejection fraction less than
20%. We refer to the smallest set of background factors that, together with
A = 0, are sufficient to produce the outcome as U
2
. The simultaneous absence
of treatment (A = 0) and presence of low ejection fraction (U
2
= 1) is another
sufficient cause of the outcome Y .
Finally, suppose there are some individuals who have neither U
1
nor U
2
and that would have developed the outcome whether they had been treated or
untreated. The existence of these “doomed” individuals implies that there are
some other background factors that are themselves sufficient to bring about
the outcome. As an oversimplified example, suppose that all individuals with
pancreatic cancer at the start of the study will die. We refer to the smallest setBy definition of background factors,
the dichotomous variables U can-
not be intervened on, and cannot
be affected by treatment A.
of background factors that are sufficient to produce the outcome regardless of
treatment status as U
0
. The presence of pancreatic cancer (U
0
= 1) is another
sufficient cause of the outcome Y .
We described 3 sufficient causes for the outcome: treatment A = 1 in
the presence of U
1
, no treatment A = 0 in the presence of U
2
, and presence
of U
0
regardless of treatment status. Each sufficient cause has one or more
components A = 1 and U
1
= 1 in the first sufficient cause. Figure 5.1 represents
each sufficient cause by a circle and its components as sections of the circle.
The term sufficient-component causes is often used to refer to the sufficient
causes and their components.
64 Interaction
Figure 5.1
The graphical representation of sufficient-component causes helps visualize a
key consequence of effect modification: as discussed in Chapter 4, the magni-
tude of the causal effect of treatment A depends on the distribution of effect
modifiers. Imagine two hypothetical scenarios. In the first one, the population
includes only 1% of individuals with U
1
= 1 (i.e., allergy to anesthesia). In
the second one, the population includes 10% of individuals with U
1
= 1. The
distribution of U
2
and U
0
is identical between these two populations. Now,
separately in each population, we conduct a randomized experiment of heart
transplant A in which half of the population is assigned to treatment A = 1.
The average causal effect of heart transplant A on death will be greater in the
second population because there are more individuals susceptible to develop
the outcome if treated. One of the 3 sufficient causes, A = 1 plus U
1
= 1, is
10 times more common in the second population than in the first one, whereas
the other two sufficient causes are equally frequent in both populations.
The graphical representation of sufficient-component causes also helps vi-
sualize an alternative concept of interaction, which is described in the next
section. First we need to describe the sufficient causes for two treatments A
and E. Consider our vitamins and heart transplant example. We have al-
ready described 3 sufficient causes of death: presence/absence of A (or E) is
irrelevant, presence of transplant A regardless of vitamins E, and absence of
transplant A regardless of vitamins E. In the case of two treatments we need
to add 2 more ways to die: presence of vitamins E regardless of transplant A,
and absence of vitamins regardless of transplant A. We also need to add four
more sufficient causes to accommodate those who would die only under certain
combination of values of the treatments A and E. Thus, depending on which
background factors are present, there are 9 possible ways to die:
Greenland and Poole (1988) first
enumerated these 9 sufficient
causes.
1. by treatment A (treatment E is irrelevant)
2. by the absence of treatment A (treatment E is irrelevant)
3. by treatment E (treatment A is irrelevant)
4. by the absence of treatment E (treatment A is irrelevant)
5. by both treatments A and E
6. by treatment A and the absence of E
7. by treatment E and the absence of A
8. by the absence of both A and E
9. by other mechanisms (both treatments A and E are irrelevant)
In other words, there are 9 possible sufficient causes with treatment com-
ponents A = 1 only, A = 0 only, E = 1 only, E = 0 only, A = 1 and E = 1,
A = 1 and E = 0, A = 0 and E = 1, A = 0 and E = 0, and neither A nor
E matter. Each of these sufficient causes includes a set of background factors
from U
1
,..., U
8
and U
0
. Figure 5.2 represents the 9 sufficient-component causes
for two treatments A and E.
5.5 Sufficient cause interaction 65
Figure 5.2
Not all 9 sufficient-component causes for a dichotomous outcome and two
treatments exist in all settings. For example, if receiving vitamins E = 1 doesThis graphical representation of
sufficient-component causes is of-
ten referred to as “the causal pies.”
not kill any individual, regardless of her treatment A, then the 3 sufficient
causes with the component E = 1 will not be present. The existence of those
3 sufficient causes would mean that some individuals (e.g., those with U
3
= 1)
would be killed by receiving vitamins (E = 1), that is, their death would be
prevented by not giving vitamins (E = 0) to them.
5.5 Sufficient cause interaction
The colloquial use of the term “interaction between treatments A and E”
evokes the existence of some causal mechanism by which the two treatments
work together (i.e., “interact”) to produce certain outcome. Interestingly, the
definition of interaction within the counterfactual framework does not require
any knowledge about those mechanisms nor even that the treatments work
together (see Fine Point 5.3). In our example of vitamins E and heart trans-
plant A, we said that there is an interaction between the treatments A and
E if the causal effect of A when everybody receives E is different from the
causal effect of A when nobody receives E. That is, interaction is defined
by the contrast of counterfactual quantities, and can therefore be identified
by conducting an ideal randomized experiment in which the conditions of ex-
changeability, positivity, and consistency hold for both treatments A and E.
There is no need to contemplate the causal mechanisms (physical, chemical,
biologic, sociological...) that underlie the presence of interaction.
This section describes a second concept of interaction that perhaps brings
us one step closer to the causal mechanisms by which treatments A and E
bring about the outcome. This second concept of interaction is not based on
counterfactual contrasts but rather on sufficient-component causes, and thus
we refer to it as interaction within the sufficient-component-cause framework
or, for brevity, sufficient cause interaction.
A sufficient cause interaction between A and E exists in the population if
A and E occur together in a sufficient cause. For example, suppose individuals
with background factors U
5
= 1 will develop the outcome when jointly receiving
66 Interaction
Fine Point 5.2
From counterfactuals to sufficient-component causes, and vice versa. There is a correspondence between the
counterfactual response types and the sufficient component causes. In the case of a dichotomous treatment and outcome,
suppose an individual has none of the background factors U
0
, U
1
, U
2
. She will have an “immune” response type because
she lacks the components necessary to complete all of the sufficient causes, whether she is treated or not. The table
below displays the mapping between response types and sufficient-component causes in the case of one treatment A.
Type Y
a=0
Y
a=1
Component causes
Doomed 1 1 U
0
= 1 or {U
1
= 1 and U
2
= 1}
Helped 1 0 U
0
= 0 and U
1
= 0 and U
2
= 1
Hurt 0 1 U
0
= 0 and U
1
= 1 and U
2
= 0
Immune 0 0 U
0
= 0 and U
1
= 0 and U
2
= 0
A particular combination of component causes corresponds to one and only one counterfactual type. However, a
particular response type may correspond to several combinations of component causes. For example, individuals of the
“doomed” type may have any combination of component causes including U
0
= 1, no matter what the values of U
1
and U
2
are, or any combination including {U
1
= 1 and U
2
= 1}.
Sufficient-component causes can also be used to provide a mechanistic description of exchangeability Y
a
`
A. For
a dichotomous treatment and outcome, exchangeability means that the proportion of individuals who would have the
outcome under treatment, and under no treatment, is the same in the treated A = 1 and the untreated A = 0. That
is, Pr[Y
a=1
= 1|A = 1] = Pr[Y
a=1
= 1|A = 0] and Pr[Y
a=0
= 1|A = 1] = Pr[Y
a=0
= 1|A = 0].
Now the individuals who would develop the outcome if treated are the “doomed” and the “hurt”, i.e., those with
U
0
= 1 or U
1
= 1. The individuals who would get the outcome if untreated are the “doomed” and the “helped”, that is,
those with U
0
= 1 or U
2
= 1. Therefore there will be exchangeability if the proportions of “doomed” + “hurt” and of
“doomed” + “helped” are equal in the treated and the untreated. That is, exchangeability for a dichotomous treatment
and outcome can be expressed in terms of sufficient-component causes as Pr[U
0
= 1 or U
1
= 1|A = 1] = Pr[U
0
= 1 or
U
1
= 1|A = 0] and Pr[U
0
= 1 or U
2
= 1|A = 1] = Pr[U
0
= 1 or U
2
= 1|A = 0].
For additional details see Greenland and Brumback (2002), Flanders (2006), and VanderWeele and Hern´an (2006).
Some of the above results were generalized to the case of two or more dichotomous treatments by VanderWeele and
Robins (2008).
vitamins (E = 1) and heart transplant (A = 1), but not when receiving only
one of the two treatments. Then a sufficient cause interaction between A and
E exists if there exists an individual with U
5
= 1. It then follows that if
there exists an individual with counterfactual responses Y
a=1,e=1
= 1 and
Y
a=0,e=1
= Y
a=1,e=0
= 0, a sufficient cause interaction between A and E is
present.
Sufficient cause interactions can be synergistic or antagonistic. There is
synergism between treatment A and treatment E when A = 1 and E = 1
are present in the same sufficient cause, and antagonism between treatment
A and treatment E when A = 1 and E = 0 (or A = 0 and E = 1) are
present in the same sufficient cause. Alternatively, one can think of antagonism
between treatment A and treatment E as synergism between treatment A and
no treatment E (or between no treatment A and treatment E).
Unlike the counterfactual definition of interaction, sufficient cause inter-
action makes explicit reference to the causal mechanisms involving the treat-
ments A and E. One could then think that identifying the presence of sufficient
cause interaction requires detailed knowledge about these causal mechanisms.
It turns out that this is not always the case: sometimes we can conclude that
sufficient cause interaction exists even if we lack any knowledge whatsoever
5.6 Counterfactuals or sufficient-component causes? 67
Fine Point 5.3
Biologic interaction. In epidemiologic discussions, sufficient-cause interaction is commonly referred to as biologic
interaction (Rothman et al, 1980). This choice of terminology might seem to imply that, in biomedical applications,
there exist biological mechanisms through which two treatments A and E act on each other in bringing about the
outcome. However, this may not be necessarily the case as illustrated by the following example proposed by VanderWeele
and Robins (2007a).
Suppose A and E are the two alleles of a gene that produces an essential protein. Individuals with a deleterious
mutation in both alleles (A = 1 and E = 1) will lack the essential protein and die within a week after birth, whereas
those with a mutation in none of the alleles (i.e., A = 0 and E = 0) or in only one of the alleles (i.e., A = 0 and E = 1,
A = 1 and E = 0 ) will have normal levels of the protein and will survive. We would say that there is synergism between
the alleles A and E because there exists a sufficient component cause of death that includes A = 1 and E = 1. That
is, both alleles work together to produce the outcome. However, it might be argued that they do not physically act on
each other and thus that they do not interact in any biological sense.
about the sufficient causes and their components. Specifically, if the inequal-Rothman (1976) described the con-
cepts of synergism and antagonism
within the sufficient-component-
cause framework.
ities in Fine Point 5.1 hold, then there exists synergism between A and E.
That is, one can empirically check that synergism is present without ever giv-
ing any thought to the causal mechanisms by which A and E work together
to bring about the outcome. This result is not that surprising because of the
correspondence between counterfactual response types and sufficient causes
(see Fine Point 5.2), and because the above inequality is a sufficient but not a
necessary condition, i.e., the inequality may not hold even if synergism exists.
5.6 Counterfactuals or sufficient-component causes?
The sufficient-component-cause framework and the counterfactual (potential
outcomes) framework address different questions. The sufficient component
cause model considers sets of actions, events, or states of nature which together
inevitably bring about the outcome under consideration. The model gives an
account of the causes of a particular effect. It addresses the question, “Given aA counterfactual framework of cau-
sation was already hinted by Hume
(1748).
particular effect, what are the various events which might have been its cause?”
The potential outcomes or counterfactual model focuses on one particular cause
or intervention and gives an account of the various effects of that cause. In
contrast to the sufficient component cause framework, the potential outcomes
framework addresses the question, “What would have occurred if a particular
factor were intervened upon and thus set to a different level than it in fact
was?” Unlike the sufficient component cause framework, the counterfactual
framework does not require a detailed knowledge of the mechanisms by which
the factor affects the outcome.The sufficient-component-cause
framework was developed in phi-
losophy by Mackie (1965). He
introduced the concept of INUS
condition for Y : an I nsufficient
but Necessary part of a condition
which is itself Unnecessary but
exclusively Sufficient for Y .
The counterfactual approach addresses the question “what happens?” The
sufficient-component-cause approach addresses the question “how does it hap-
pen?” For the contents of this book—conditions and methods to estimate the
average causal effects of hypothetical interventions—the counterfactual frame-
work is the natural one. The sufficient-component-cause framework is helpful
to think about the causal mechanisms at work in bringing about a particular
outcome. Sufficient-component causes have a rightful place in the teaching of
causal inference because they help understand key concepts like the dependence
68 Interaction
Fine Point 5.4
More on the attributable fraction. Fine Point 3.6 defined the excess fraction for treatment A as the proportion of
cases attributable to treatment A in a particular population, and described an example in which the excess fraction for
A was 75%. That is, 75% of the cases would not have occurred if everybody had received treatment a = 0 rather than
their observed treatment A. Now consider a second treatment E. Suppose that the excess fraction for E is 50%. Does
this mean that a joint intervention on A and E could prevent 125% (75% + 50%) of the cases? Of course not.
Clearly the excess fraction cannot exceed 100% for a single treatment (either A or E). Similarly, it should be clear
that the excess fraction for any joint intervention on A and E cannot exceed 100%. That is, if we were allowed to
intervene in any way we wish (by modifying A, E, or both) in a population, we could never prevent a fraction of disease
greater than 100%. In other words, no more than 100% of the cases can be attributed to the lack of certain intervention,
whether single or joint. But then why is the sum of excess fractions for two single treatments greater than 100%? The
sufficient-component-cause framework helps answer this question.
As an example, suppose that Zeus had background factors U
5
= 1 (and none of the other background factors) and
was treated with both A = 1 and E = 1. Zeus would not have been a case if either treatment A or treatment E had
been withheld. Thus Zeus is counted as a case prevented by an intervention that sets a = 0, i.e., Zeus is part of the
75% of cases attributable to A. But Zeus is also counted as a case prevented by an intervention that sets e = 0, i.e.,
Zeus is part of the 50% of cases attributable to E. No wonder the sum of the excess fractions for A and E exceeds
100%: some individuals like Zeus are counted twice!
The sufficient-component-cause framework shows that it makes little sense to talk about the fraction of disease
attributable to A and E separately when both may be components of the same sufficient cause. For example, the
discussion about the fraction of disease attributable to either genes or environment is misleading. Consider the mental
retardation caused by phenylketonuria, a condition that appears in genetically susceptible individuals who eat certain
foods. The excess fraction for those foods is 100% because all cases can be prevented by removing the foods from
the diet. The excess fraction for the genes is also 100% because all cases would be prevented if we could replace the
susceptibility genes. Thus the causes of mental retardation can be seen as either 100% genetic or 100% environmental.
See Rothman, Greenland, and Lash (2008) for further discussion.
of the magnitude of causal effects on the distribution of background factors (ef-
fect modifiers), and the relationship between effect modification, interaction,
and synergism.
Though the sufficient-component-cause framework is useful from a peda-
gogic standpoint, its relevance to actual data analysis is yet to be determined.
In its classical form, the sufficient-component-cause framework is determinis-
tic, its conclusions depend on the coding on the outcome, and is by definition
limited to dichotomous treatments and outcomes (or to variables that can be
recoded as dichotomous variables). This limitation practically rules out the
consideration of any continuous factors, and restricts the applicability of the
framework to contexts with a small number of dichotomous factors. More
recent extensions of the sufficient-component-cause framework to stochastic
settings and to categorical and ordinal treatments might lead to an increasedVanderWeele (2010b) provided
extensions to 3-level treatments.
VanderWeele and Robins (2012)
explored the relationship between
stochastic counterfactuals and
stochastic sufficient causes.
application of this approach to realistic data analysis. Finally, even allowing for
these extensions of the sufficient-component-cause framework, we may rarely
have the large amount of data needed to study the fine distinctions it makes.
To estimate causal effects more generally, the counterfactual framework will
likely continue to be the one most often employed. Some apparently alternative
frameworks—causal diagrams, decision theory—are essentially equivalent to
the counterfactual framework, as described in the next chapter.
5.6 Counterfactuals or sufficient-component causes? 69
Technical Point 5.3
Monotonicity of causal effects and sufficient causes. When treatment A and E have monotonic effects, then some
sufficient causes are guaranteed not to exist. For example, suppose that cigarette smoking (A = 1) never prevents heart
disease, and that physical inactivity (E = 1) never prevents heart disease. Then no sufficient causes including either
A = 0 or E = 0 can be present. This is so because, if a sufficient cause including the component A = 0 existed, then
some individuals (e.g., those with U
2
= 1) would develop the outcome if they were unexposed (A = 0) or, equivalently,
the outcome could be prevented in those individuals by treating them (A = 1). The same rationale applies to E = 0.
The sufficient component causes that cannot exist when the effects of A and E are monotonic are crossed out in Figure
5.3.
Figure 5.3
70 Interaction
Chapter 6
GRAPHICAL REPRESENTATION OF CAUSAL EFFECTS
Causal inference generally requires expert knowledge and untestable assumptions about the causal network linking
treatment, outcome, and other variables. Earlier chapters focused on the conditions and methods to compute
causal effects in oversimplified scenarios (e.g., the causal effect of your looking up on other pedestrians’ behavior,
an idealized heart transplant study). The goal was to provide a gentle introduction to the ideas underlying the
more sophisticated approaches that are required in realistic settings. Because the scenarios we considered were so
simple, there was really no need to make the causal network explicit. As we start to turn our attention towards
more complex situations, however, it will become crucial to be explicit about what we know and what we assume
about the variables relevant to our particular causal inference problem.
This chapter introduces a graphical tool to represent our qualitative expert knowledge and a priori assumptions
about the causal structure of interest. By summarizing knowledge and assumptions in an intuitive way, graphs
help clarify conceptual problems and enhance communication among investigators. The use of graphs in causal
inference problems makes it easier to follow a sensible advice: draw your assumptions before your conclusions.
6.1 Causal diagrams
This chapter describes graphs, which we will refer to as causal diagrams, to
represent key causal concepts. The modern theory of diagrams for causal infer-
ence arose within the disciplines of computer science and artificial intelligence.
This and the next three chapters are focused on problem conceptualization viaComprehensive books on this sub-
ject have been written by Pearl
(2009) and Spirtes, Glymour and
Scheines (2000).
causal diagrams.
Take a look at the graph in Figure 6.1. It comprises three nodes representing
random variables (L, A, Y ) and three edges (the arrows). We adopt the
convention that time flows from left to right, and thus L is temporally prior to
A and Y , and A is temporally prior to Y . As in previous chapters, L, A, and
Y represent disease severity, heart transplant, and death, respectively.
The presence of an arrow pointing from a particular variable V to another
variable W indicates that we know there is a direct causal effect (i.e., an
effect not mediated through any other variables on the graph) for at least one
individual. Alternatively, the lack of an arrow means that we know that V has
Figure 6.1
no direct causal effect on W for any individual in the population. For example,
in Figure 6.1, the arrow from L to A means that disease severity affects the
probability of receiving a heart transplant. A standard causal diagram does
not distinguish whether an arrow represents a harmful effect or a protective
effect. Furthermore, if, as in figure 6.1, a variable (here, Y ) has two causes,
the diagram does not encode how the two causes interact.
Causal diagrams like the one in Figure 6.1 are known as directed acyclic
graphs, which is commonly abbreviated as DAGs. “Directed” because the
edges imply a direction: because the arrow from L to A is into A, L may cause
A, but not the other way around. “Acyclic” because there are no cycles: a
variable cannot cause itself, either directly or through another variable.
Directed acyclic graphs have applications other than causal inference. Here
72 Graphical representation of causal effects
Technical Point 6.1
Causal directed acyclic graphs. We define a directed acyclic graph (DAG) G to be a graph whose nodes (vertices)
are random variables V = (V
1
, . . . , V
M
) with directed edges (arrows) and no directed cycles. We use P A
m
to denote
the parents of V
m
, i.e., the set of nodes from which there is a direct arrow into V
m
. The variable V
m
is a descendant
of V
j
(and V
j
is an ancestor of V
m
) if there is a sequence of nodes connected by edges between V
j
and V
m
such that,
following the direction indicated by the arrows, one can reach V
m
by starting at V
j
. For example, consider the DAG in
Figure 6.1. In this DAG, M = 3 and we can choose V
1
= L, V
2
= A, and V
3
= Y ; the parents P A
3
of V
3
= Y are
(L, A). We will adopt the ordering convention that if m > j, V
m
is not an ancestor of V
j
. We define the distribution of
V to be Markov with respect to a DAG G (equivalently, the distribution factors according to a DAG G) if, for each j,
V
j
is independent of its non-descendants conditional on its parents. This latter statement is mathematically equivalent
to the statement that the density f (V ) of the variables V in DAG G satisfies the Markov factorization
f (v) =
M
Y
j=1
f (v
j
| pa
j
) .
A causal DAG is a DAG in which 1) the lack of an arrow from node V
j
to V
m
(i.e., V
j
is not a parent of V
m
) can
be interpreted as the absence of a direct causal effect of V
j
on V
m
relative to the other variables on the graph, 2) all
common causes, even if unmeasured, of any pair of variables on the graph are themselves on the graph, and 3) any
variable is a cause of its descendants. Causal DAGs are of no practical use unless we make an assumption linking the
causal structure represented by the DAG to the data obtained in a study. This assumption, referred to as the causal
Markov assumption, states that, conditional on its direct causes, a variable V
j
is independent of any variable for which
it is not a cause. That is, conditional on its parents, V
j
is independent of its non-descendants; hence, a causal DAG is
Markov with respect to the DAG G.
we focus on causal directed acyclic graphs. A defining property of causal DAGs
is that, conditional on its direct causes, any variable on the DAG is independent
of any other variable for which it is not a cause. This assumption, referred to
as the causal Markov assumption, implies that in a causal DAG the common
causes of any pair of variables in the graph must be also in the graph. For a
formal definition of causal DAGs, see Technical Point 6.1.
For example, suppose in our study individuals are randomly assigned to
heart transplant A with a probability that depends on the severity of their
disease L. Then L is a common cause of A and Y , and needs to be included
in the graph, as shown in the causal diagram in Figure 6.1. Now suppose
Figure 6.2
in our study all individuals are randomly assigned to heart transplant with
the same probability regardless of their disease severity. Then L is not a
common cause of A and Y and need not be included in the causal diagram.
Figure 6.1 represents a conditionally randomized experiment, whereas Figure
6.2 represents a marginally randomized experiment.
Figure 6.1 may also represent an observational study. Specifically, Figure
6.1 represents an observational study in which we are willing to assume that
the assignment of heart transplant A has as parent disease severity L and no
other causes of Y . Otherwise, those causes of Y , even if unmeasured, would
need to be included in the diagram, as they would be common causes of A and
Y . In the next chapter we will describe how the willingness to consider Figure
6.1 as the causal diagram for an observational study is the graphic translation
of the assumption of conditional exchangeability given L, Y
a
⊥⊥A|L for all a.
Many people find the graphical approach to causal inference easier to use
and more intuitive than the counterfactual approach. However, the two ap-
6.2 Causal diagrams and marginal independence 73
Technical Point 6.2
Counterfactual models associated with a causal DAG. In this book, a causal DAG G represents an underlying
counterfactual model. To provide a formal definition of the counterfactual model represented by a DAG G, we use the
following notation. For any random variable W , let W denote the support (i.e., the set of possible values w) of W . For
any set of ordered variables W
1
, . . . , W
m
, define w
m
= (w
1
, . . . , w
m
). Let R denote any subset of variables in V and
let r be a value of R. Then V
r
m
denotes the counterfactual value of V
m
when R is set to r.
A nonparametric structural equation model (NPSEM) represented by a DAG G with vertex set V = (V
1
, V
2
.., V
M
)
(ordered such that if i < j then V
i
is not a descendant of V
j
) assumes the existence of unobserved random variables
(errors) ϵ
m
and deterministic unknown functions f
m
(pa
m
, ϵ
m
) such that V
1
= f
1
(ϵ
1
) and the one-step ahead counter-
factual V
v
m−1
m
≡ V
pa
m
m
is given by f
m
(pa
m
, ϵ
m
). That is, only the parents of V
m
have a direct effect on V
m
relative to
the other variables on G. An NPSEM implies that any variable V
j
on the graph can be intervened on, as counterfactuals
in which V
j
has been set to a specific value v
j
are assumed to exist. Both the factual variable V
m
and the counterfactuals
V
r
m
for any R ⊂ V are obtained recursively from V
1
and V
v
j−1
j
, M ≥ j > 1. For example, V
v
1
3
= V
v
1
,V
v
1
2
3
, i.e., the
counterfactual value V
v
1
3
of V
3
when V
1
is set to v
1
is the one-step ahead counterfactual V
v
1
,v
2
3
with v
2
equal to the
counterfactual value V
v
1
2
of V
2
. Similarly, V
3
= V
V
1
,V
V
1
2
3
and V
v
1
,v
4
3
= V
v
1
3
because V
4
is not a direct cause of V
3
. The
absence of an arrow from V
j
to V
k
implies that V
j
is not a direct cause of V
k
for any individual.
Robins (1986) introduced this NPSEM, referred to it as a finest causally interpreted structural tree graph (FCISTG)
“as detailed as the data”, and referred to the parents P A
m
of V
m
as causal risk factors for V
m
controlling for the earlier
variables in the ordering. Pearl (2009) showed how to represent this model with a DAG. Robins (1986) also proposed
often more realistic causally interpreted structural tree graphs in which only a subset of the variables are subject to
intervention. For expositional purposes, we will generally assume that every variable can be intervened on, even though
the statistical methods considered here do not actually require this assumption.
proaches are intimately linked. Specifically, associated with each graph is an
underlying counterfactual model (see Technical Points 6.2 and 6.3). It is this
model that provides the mathematical justification for the heuristic, intuitive
graphical methods we now describe. However, conventional causal diagrams
do not include the underlying counterfactual variables on the graph. Therefore
the link between graphs and counterfactuals has traditionally remained hidden.
A recently developed type of causal directed acyclic graph—the Single World
Intervention Graph (SWIG)—seamlessly unifies the counterfactual and graph-Richardson and Robins (2013) de-
veloped the Single World Interven-
tion Graph (SWIG).
ical approaches to causal inference by explicitly including the counterfactual
variables on the graph. We defer the introduction of SWIGs until Chapter 7
as the material covered in this chapter serves as a necessary prerequisite.
Causal diagrams are a simple way to encode our subject-matter knowledge,
and our assumptions, about the qualitative causal structure of a problem. But,
as described in the next sections, causal diagrams also encode information
about potential associations between the variables in the causal network. It
is precisely this simultaneous representation of association and causation that
makes causal diagrams such an attractive tool. What follows is an informal
introduction to graphic rules to infer associations from causal diagrams. Our
emphasis is on conceptual insight rather than on formal rigor.
6.2 Causal diagrams and marginal independence
Consider the following two examples. First, suppose you know that aspirin use
A has a preventive causal effect on the risk of heart disease Y , i.e., Pr[Y
a=1
=
74 Graphical representation of causal effects
Technical Point 6.3
Independencies associated with counterfactual models. An FCISTG model does not imply that the causal Markov
assumption of Technical Point 6.1 holds; additional statistical independence assumptions are needed. For example, Pearl
(2000) usually assumed an NPSEM in which all error terms ϵ
m
are mutually independent. We refer to Pearl’s model
with independent errors as an NPSEM-IE. In contrast, Robins (1986) only assumed that, given any v
M
, the one-step
ahead counterfactuals V
v
m−1
m
= f
m
(pa
m
, ϵ
m
) for m = 1, ..M are jointly independent where v
m−1
is a subvector of the
v
M
, and referred to this as the finest fully randomized causally interpreted structured tree graph (FFRCISTG) model as
detailed as the data.
More precisely, Robins (1986) made the assumption that for each m, conditional on the factual past V
m−1
= v
m−1
,
any future evolution from m + 1 of one-step ahead counterfactuals (consistent with v
m−1
) is independent of the factual
variable V
m
. Robins and Richardson (2010) showed that this assumption is equivalent to the assumption of the previous
paragraph for a positive distribution. In the absence of positivity, we define the model as in the last paragraph.
Robins (1986) showed his independence assumption implies that the causal Markov assumption holds. An NPSEM-
IE is an FFRCISTG but not vice-versa because an NPSEM-IE makes many more independence assumptions than an
FFRCISTG (Robins and Richardson 2010).
Unless stated otherwise, a DAG represents an NPSEM but we may need to specify which type. For example, the
DAG in Figure 6.2 may correspond to either an NPSEM-IE that implies full exchangeability
Y
a=0
, Y
a=1
⊥⊥A, or to
an FFRCISTG that only implies marginal exchangeability Y
a
⊥⊥A for both a = 0 and a = 1. We will assume that a
causal DAG represents an FFRCISTG as detailed as the data whenever we do not mention the underlying model.
1] = Pr[Y
a=0
= 1]. The causal diagram in Figure 6.2 is the graphical transla-
tion of this knowledge for an experiment in which aspirin A is randomly, and
unconditionally, assigned. Second, suppose you know that carrying a lighter A
has no causal effect (causative or preventive) on anyone’s risk of lung cancer Y ,
i.e., Pr[Y
a=1
= 1] = Pr[Y
a=0
= 1], and that cigarette smoking L has a causal
effect on both carrying a lighter A and lung cancer Y . The causal diagram in
Figure 6.3 is the graphical translation of this knowledge. The lack of an arrow
Figure 6.3
between A and Y indicates that carrying a lighter does not have a causal effect
on lung cancer; L is depicted as a common cause of A and Y .
To draw Figures 6.2 and 6.3 we only used your knowledge about the causal
relations among the variables in the diagram but, interestingly, these causal
diagrams also encode information about the expected associations (or, more
exactly, the lack of them) among the variables in the diagram. We now argue
heuristically that, in general, the variables A and Y will be associated in both
Figure 6.2 and 6.3, and describe key related results from causal graphs theory.
Take first the randomized experiment represented in Figure 6.2. Intuitively
one would expect that two variables A and Y linked only by a causal arrow
would be associated. And that is exactly what causal graphs theory shows:
when one knows that A has a causal effect on Y , as in Figure 6.2, then oneA path between two variables R and
S in a DAG is a route that connects
R and S by following a sequence
of edges such that the route vis-
its no variable more than once. A
path is causal if it consists entirely
of edges with their arrows pointing
in the same direction. Otherwise it
is noncausal.
should also generally expect A and Y to be associated. This is of course
consistent with the fact that, in an ideal randomized experiment with un-
conditional exchangeability, causation Pr[Y
a=1
= 1] = Pr[Y
a=0
= 1] implies
association Pr[Y = 1|A = 1] = Pr[Y = 1|A = 0], and vice versa. A heuristic
that captures the causation-association correspondence in causal diagrams is
the visualization of the paths between two variables as pipes or wires through
which association flows. Association, unlike causation, is a symmetric relation-
ship between two variables; thus, when present, association flows between two
variables regardless of the direction of the causal arrows. In Figure 6.2 one
could equivalently say that the association flows from A to Y or from Y to A.
6.2 Causal diagrams and marginal independence 75
Now let us consider the observational study represented in Figure 6.3. We
know that carrying a lighter A has no causal effect on lung cancer Y . The
question now is whether carrying a lighter A is associated with lung cancer Y .
That is, we know that Pr[Y
a=1
= 1] = Pr[Y
a=0
= 1] but is it also true that
Pr[Y = 1|A = 1] = Pr[Y = 1|A = 0]? To answer this question, imagine that a
naive investigator decides to study the effect of carrying a lighter A on the risk
of lung cancer Y (we do know that there is no effect but this is unknown to
the investigator). He asks a large number of people whether they are carrying
lighters and then records whether they are diagnosed with lung cancer during
the next 5 years. Hera is one of the study participants. We learn that Hera
is carrying a lighter. But if Hera is carrying a lighter (A = 1), then it is
more likely that she is a smoker (L = 1), and therefore she has a greater than
average risk of developing lung cancer (Y = 1). We then intuitively conclude
that A and Y are expected to be associated because the cancer risk in those
carrying a lighter (A = 1) is different from the cancer risk in those not carrying
a lighter (A = 0), or Pr[Y = 1|A = 1] = Pr[Y = 1|A = 0]. In other words,
having information about the treatment A improves our ability to predict the
outcome Y , even though A does not have a causal effect on Y . The investigator
will make a mistake if he concludes that A has a causal effect on Y just because
A and Y are associated. Causal graphs theory again confirms our intuition. In
graphic terms, A and Y are associated because there is a flow of association
from A to Y (or, equivalently, from Y to A) through the common cause L.
Let us now consider a third example. Suppose you know that certain genetic
haplotype A has no causal effect on anyone’s risk of becoming a cigarette
smoker Y , i.e., Pr[Y
a=1
= 1] = Pr[Y
a=0
= 1], and that both the haplotype A
and cigarette smoking Y have a causal effect on the risk of heart disease L.
Figure 6.4
The causal diagram in Figure 6.4 is the graphical translation of this knowledge.
The lack of an arrow between A and Y indicates that the haplotype does not
have a causal effect on cigarette smoking, and L is depicted as a common
effect of A and Y . The common effect L is referred to as a collider on the path
A → L ← Y because two arrowheads collide on this node.
Again the question is whether A and Y are associated. To answer this
question, imagine that another investigator decides to study the effect of hap-
lotype A on the risk of becoming a cigarette smoker Y (we do know that there
is no effect but this is unknown to the investigator). She makes genetic de-
terminations on a large number of children, and then records whether they
end up becoming smokers. Apollo is one of the study participants. We learn
that Apollo does not have the haplotype (A = 0). Is he more or less likely
to become a cigarette smoker (Y = 1) than the average person? Learning
about the haplotype A does not improve our ability to predict the outcome Y
because the risk in those with (A = 1) and without (A = 0) the haplotype is
the same, or Pr[Y = 1|A = 1] = Pr[Y = 1|A = 0]. In other words, we would
intuitively conclude that A and Y are not associated, i.e., A and Y are inde-
pendent or A⊥⊥Y . The knowledge that both A and Y cause heart disease L is
irrelevant when considering the association between A and Y . Causal graphs
theory again confirms our intuition because it says that colliders, unlike other
variables, block the flow of association along the path on which they lie. Thus
A and Y are independent because the only path between them, A → L ← Y ,
is blocked by the collider L.
In summary, two variables are (marginally) associated if one causes the
other, or if they share common causes. Otherwise they will be (marginally) in-
dependent. The next section explores the conditions under which two variables
A and Y may be independent conditionally on a third variable L.
76 Graphical representation of causal effects
6.3 Causal diagrams and conditional independence
We now revisit the settings depicted in Figures 6.2, 6.3, and 6.4 to discuss the
concept of conditional independence in causal diagrams.
According to Figure 6.2, we expect aspirin A and heart disease Y to be
associated because aspirin has a causal effect on heart disease. Now suppose
we obtain an additional piece of information: aspirin A affects the risk of heart
disease Y because it reduces platelet aggregation B. This new knowledge is
Figure 6.5
translated into the causal diagram of Figure 6.5 that shows platelet aggregation
B (1: high, 0: low) as a mediator of the effect of A on Y .
Once a third variable is introduced in the causal diagram we can ask a new
question: is there an association between A and Y within levels of (conditional
on) B? Or, equivalently: when we already have information on B, does infor-
mation about A improve our ability to predict Y ? To answer this question,
suppose data were collected on A, B, and Y in a large number of individuals,
and that we restrict the analysis to the subset of individuals with low platelet
aggregation (B = 0). The square box placed around the node B in Figure 6.5
represents this restriction. (We would also draw a box around B if the analysis
were restricted to the subset of individuals with B = 1.)Because no conditional indepen-
dences are expected in complete
causal diagrams (those in which all
possible arrows are present), it is of-
ten said that information about as-
sociations is in the missing arrows.
Individuals with low platelet aggregation (B = 0) have a lower than average
risk of heart disease. Now take one of these individuals. Regardless of whether
the individual was treated (A = 1) or untreated (A = 0), we already knew
that he has a lower than average risk because of his low platelet aggregation.
In fact, because aspirin use affects heart disease risk only through platelet
aggregation, learning an individual’s treatment status does not contribute any
additional information to predict his risk of heart disease. Thus, in the subset of
individuals with B = 0, treatment A and outcome Y are not associated. (The
same informal argument can be made for individuals in the group with B = 1.)
Even though A and Y are marginally associated, A and Y are conditionally
independent (unassociated) given B because the risk of heart disease is the
same in the treated and the untreated within levels of B: Pr[Y = 1|A =
1, B = b] = Pr[Y = 1|A = 0, B = b] for all b. That is, A⊥⊥Y |B. Graphically,
we say that a box placed around variable B blocks the flow of association
through the path A → B → Y .
Let us now return to Figure 6.3. We concluded in the previous section that
carrying a lighter A was associated with the risk of lung cancer Y because
the path A ← L → Y was open to the flow of association from A to Y . The
question we ask now is whether A is associated with Y conditional on L. This
Figure 6.6 new question is represented by the box around L in Figure 6.6. Suppose the
investigator restricts the study to nonsmokers (L = 0). In that case, learning
that an individual carries a lighter (A = 1) does not help predict his risk of
lung cancer (Y = 1) because the entire argument for better prediction relied
on the fact that people carrying lighters are more likely to be smokers. This
argument is irrelevant when the study is restricted to nonsmokers or, more
generally, to people who smoke with a particular intensity. Even though A
and Y are marginally associated, A and Y are conditionally independent givenBlocking the flow of association
between treatment and outcome
through the common cause is
the graph-based justification to
use stratification as a method to
achieve exchangeability.
L because the risk of lung cancer is the same in the treated and the untreated
within levels of L: Pr[Y = 1|A = 1, L = l] = Pr[Y = 1|A = 0, L = l] for all
l. That is, A⊥⊥Y |L. Graphically, we say that the flow of association between
A and Y is interrupted because the path A ← L → Y is blocked by the box
around L.
Finally, consider Figure 6.4 again. We concluded in the previous section
that having the haplotype A was independent of being a cigarette smoker
6.4 Positivity and consistency in causal diagrams 77
Y because the path between A and Y , A → L ← Y , was blocked by the
collider L. We now argue heuristically that, in general, A and Y will be
conditionally associated within levels of their common effect L. Suppose that
the investigators, who are interested in estimating the effect of haplotype A
on smoking status Y , restricted the study population to individuals with heart
disease (L = 1). The square around L in Figure 6.7 indicates that they are
conditioning on a particular value of L. Knowing that an individual with heart
disease lacks haplotype A provides some information about her smoking status
Figure 6.7 because, in the absence of A, it is more likely that another cause of L such
as Y is present. That is, among people with heart disease, the proportion of
smokers is increased among those without the haplotype A. Therefore, A and
Y are inversely associated conditionally on L = 1. The investigator will make a
mistake if he concludes that A has a causal effect on Y just because A and Y are
associated within levels of L. In the extreme, if A and Y were the only causesSee Chapter 8 for more on associ-
ations due to conditioning on com-
mon effects.
of L, then among people with heart disease the absence of one of them would
perfectly predict the presence of the other. Causal graphs theory shows that
indeed conditioning on a collider like L opens the path A → L ← Y , which
was blocked when the collider was not conditioned on. Intuitively, whether
two variables (the causes) are associated cannot be influenced by an event
in the future (their effect), but two causes of a given effect generally become
associated once we stratify on the common effect.
As another example, the causal diagram in Figure 6.8 adds to that in Figure
Figure 6.8
6.7 a diuretic medication C whose use is a consequence of a diagnosis of heart
disease. A and Y are also associated within levels of C because C is a common
effect of A and Y . Causal graphs theory shows that conditioning on a variable
C affected by a collider L also opens the path A → L ← Y . This path is blocked
in the absence of conditioning on either the collider L or its consequence C.
This and the previous section review three structural reasons why two vari-
ables may be associated: one causes the other, they share common causes, or
they share a common effect and the analysis is restricted to certain level of
that common effect (or of its descendants). Along the way we introduced aThe mathematical theory underly-
ing the graphical rules is known as
“d-separation” (Pearl 1995).
number of graphical rules that can be applied to any causal diagram to deter-
mine whether two variables are (conditionally) independent. The arguments
we used to support these graphical rules were heuristic and relied on our causal
intuitions. These arguments, however, have been formalized and mathemat-
ically proven. See Fine Point 6.1 for a systematic summary of the graphical
rules, and Fine Point 6.2 for an introduction to the concept of faithfulness.
Figure 6.9
There is another possible source of association between two variables that
we have not discussed yet: chance or random variability. Unlike the structural
reasons for an association between two variables—causal effect of one on the
other, shared common causes, conditioning on common effects—random vari-
ability results in chance associations that become smaller when the size of the
study population increases.
To focus our discussion on structural associations rather than chance asso-
ciations, we continue to assume until Chapter 10 that we have recorded data on
every individual in a very large (perhaps hypothetical) population of interest.
6.4 Positivity and consistency in causal diagrams
Because causal diagrams encode our qualitative expert knowledge about the
causal structure, they can be used as a visual aid to help conceptualize causal
78 Graphical representation of causal effects
Fine Point 6.1
D-separation. We define a path to be either blocked or open according to the following graphical rules.
1. If there are no variables being conditioned on, a path is blocked if and only if two arrowheads on the path collide
at some variable on the path. In Figure 6.1, the path L → A → Y is open, whereas the path A → Y ← L is
blocked because two arrowheads on the path collide at Y . We call Y a collider on the path A → Y ← L.
2. Any path that contains a non-collider that has been conditioned on is blocked. In Figure 6.5, the path between
A and Y is blocked after conditioning on B. We use a square box around a variable to indicate that we are
conditioning on it.
3. A collider that has been conditioned on does not block a path. In Figure 6.7, the path between A and Y is open
after conditioning on L.
4. A collider that has a descendant that has been conditioned on does not block a path. In Figure 6.8, the path
between A and Y is open after conditioning on C, a descendant of the collider L.
Rules 1–4 can be summarized as follows. A path is blocked if and only if it contains a non-collider that has been
conditioned on, or it contains a collider that has not been conditioned on and has no descendants that have been
conditioned on. Two variables are d-separated if all paths between them are blocked (otherwise they are d-connected).
Two sets of variables are d-separated if each variable in the first set is d-separated from every variable in the second set.
Thus, A and L are not d-separated in Figure 6.1 because there is one open path between them (L → A), despite the
other path (A → Y ← L)’s being blocked by the collider Y . In Figure 6.4, however, A and Y are d-separated because
the only path between them is blocked by the collider L.
The relationship between statistical independence and the purely graphical concept of d-separation relies on the
causal Markov assumption (Technical Point 6.1): In a causal DAG, any variable is independent of its non-descendants
conditional on its parents. Pearl (1988) proved the following fundamental theorem: The causal Markov assumption
implies that, given any three disjoint sets A, B, C of variables, if A is d-separated from B conditional on C, then A
is statistically independent of B given C. The assumption that the converse holds, i.e., that A is d-separated from B
conditional on C if A is statistically independent of B given C, is a separate assumption—the faithfulness assumption
described in Fine Point 6.2. Under faithfulness, A is conditionally independent of Y given B in Figure 6.5, A is not
conditionally independent of Y given L in Figure 6.7, and A is not conditionally independent of Y given C in Figure
6.8. The d-separation rules (‘d-’ stands for directional) to infer associational statements from causal diagrams were
formalized by Pearl (1995). An equivalent set of graphical rules, known as “moralization”, was developed by Lauritzen
et al. (1990).
problems and guide data analyses. In fact, the formulas that we described in
Chapter 2 to quantify treatment effects—standardization and IP weighting—
can also be derived using causal graphs theory, as part of what is sometimes
referred to as the do-calculus. Therefore, our choice of counterfactual theoryPearl (2009) reviews quantitative
methods for causal inference that
are derived from graph theory.
in Chapters 1-5 did not really privilege one particular approach but only one
particular notation.
Regardless of the notation used (counterfactuals or graphs), exchangeabil-
ity, positivity, and consistency are conditions required for causal inference via
standardization or IP weighting. If any of these conditions does not hold, the
numbers arising from the data analysis may not be appropriately interpreted
as measures of causal effect. In the next section (and in Chapters 7 and 8) we
discuss how the exchangeability condition is translated into graph language.
Here we focus on positivity and consistency.
Unfortunately, causal graphs cannot encode violations of positivity except
in special cases, e.g, when positivity is violated because a treatment A hap-
6.4 Positivity and consistency in causal diagrams 79
Fine Point 6.2
Faithfulness. In a causal DAG the absence of an arrow from A to Y indicates that the sharp null hypothesis of no
causal effect of A on any individual’s Y holds, and an arrow A → Y (as in Figure 6.2) indicates that A has a causal
effect on the outcome Y of at least one individual in the population. Thus, we would generally expect that, under
Figure 6.2, the average causal effect of A on Y , Pr[Y
a=1
= 1] −Pr[Y
a=0
= 1], and the association between A and Y ,
Pr[Y = 1|A = 1] −Pr[Y = 1|A = 0], are not null. However, that is not necessarily true: a setting represented by Figure
6.2 may be one in which there is neither an average causal effect nor an association. For an example, remember the
data in Table 4.1. Heart transplant A increases the risk of death Y in women (half of the population) and decreases the
risk of death in men (the other half). Because the beneficial and harmful effects of A perfectly cancel out, the average
causal effect is null, Pr[Y
a=1
= 1] = Pr[Y
a=0
= 1]. Yet Figure 6.2 is the correct causal diagram because treatment A
affects the outcome Y of some individuals—in fact, of all individuals—in the population.
Formally, faithfulness is the assumption that, for three disjoint sets A, B, C on a causal DAG (where C may be the
empty set), A independent of B given C implies A is d-separated from B given C. When, as in our example, the causal
diagram makes us expect a non-null association that does not actually exist in the data, we say that the joint distribution
of the data is not faithful to the causal DAG. In our example the unfaithfulness was the result of effect modification
(by sex) with opposite effects of exactly equal magnitude in each half of the population. Such perfect cancellation of
effects is rare, and thus we will assume faithfulness throughout this book. Because unfaithful distributions are rare, in
practice lack of d-separation (See Fine Point 6.1) can be almost always equated to non-zero association.
There are, however, instances in which faithfulness is violated by design. For example, consider the prospective study
in Section 4.5. The average causal effect of A on Y was computed after matching on L. In the matched population, L
and A are not associated because the distribution of L is the same in the treated and the untreated. That is, individuals
are selected into the matched population because they have a particular combination of values of L and A. The causal
diagram in Figure 6.9 represents the setting of a matched study in which selection S (1: yes, 0: no) is determined by
both A and L. The box around S indicates that the analysis is restricted to those selected into the matched cohort
(S = 1). According to d-separation rules, there are two open paths between A and L when conditioning on S: L → A
and L → S ← A. Thus one would expect L and A to be associated conditionally on S. However, matching ensures
that L and A are not associated (see Chapter 4). Why the discrepancy? Matching creates an association via the path
L → S ← A that is of equal magnitude, but opposite direction, as the association via the path L → A. The net result
is a perfect cancellation of the associations. Matching leads to unfaithfulness.
Finally, faithfulness may be violated when there exist deterministic relations between variables on the graph. Specifi-
cally, when two variables are linked by paths that include deterministic arrows, then the two variables are independent
if all paths between them are blocked, but might also be independent even if some paths are open. In this book we
will assume faithfulness unless we say otherwise. Faithfulness is also assumed when the goal of the data analysis is
discovering the causal structure (see Fine Point 6.3)
pens to be a deterministic function of a pretreatment variable L. In this case,
we bold the L → A arrow to indicate determinism. The first component of
consistency—well-defined interventions—means that the arrow from treatment
A to outcome Y corresponds to a possibly hypothetical but relatively unam-
biguous intervention. In the causal diagrams discussed in this book, positivity
is implicit unless otherwise specified, and consistency is embedded in the no-
tation because we only consider treatment nodes with relatively well-defined
interventions. Note that positivity is concerned with arrows into the treatment
nodes, and well-defined interventions are only concerned with arrows leaving
the treatment nodes.
Thus, the treatment nodes are implicitly given a different status compared
with all other nodes. Some authors make this difference explicit by including
decision nodes in causal diagrams. Though this decision-theoretic approach
largely leads to the same methods described here, we do not include decision
80 Graphical representation of causal effects
nodes in the causal diagrams presented in this chapter. Because we are always
explicit about the potential interventions on the variable A, the additional
nodes (to represent the potential interventions) would be somewhat redun-Influence diagrams are causal di-
agrams augmented with decision
nodes to represent the interventions
of interest (Dawid 2000, 2002).
dant. However, we will give a different status to treatment nodes when using
SWIGs—causal diagrams with nodes representing counterfactual variables—in
subsequent chapters.
The different status of treatment nodes compared with other nodes was also
graphically explicit in the causal trees introduced in Chapter 2, in which non-
treatment branches corresponding to non-treatment variables L and Y were
enclosed in circles, and in the “pies” representing sufficient causes in Chapter
5, which distinguish between potential treatments A and E and background
factors U. Also, our discussion on sufficiently well-defined interventions of
treatment in Chapter 3 emphasizes the requirements imposed on the treatment
variables A that do not apply to other variables.
In contrast, the causal diagrams in this chapter apparently assign the same
status to all variables in the diagram—this is indeed the case when causal dia-
grams are considered as representations of nonparametric structural equations
models with independent errors (see Technical Point 6.2). The apparentlyRecently, Pearl (2018, 2019) has
suggested a concept of causation
based on variables that “listen to
others,” which continues to assume
that for every variable there are
well-defined counterfactuals.
equal status of all variables in causal diagrams may be misleading because
some of those variables correspond to ill-defined interventions. It may be okay
to draw a causal diagram that includes a node for “obesity” as the outcome
Y or even as a covariate L (more about this on Section 9.5). However, for the
reasons discussed in Chapter 3, it is generally not okay to draw a causal dia-
gram that includes a node for “obesity” as a treatment A. In causal diagrams,
nodes for treatment variables need to correspond to sufficiently well-defined
interventions.
For example, suppose that we are interested in the potential causal effect
of “weight loss” A on mortality Y , as discussed in Chapter 3. The causal
diagram in Figure 6.10 includes nodes for A and Y as well as nodes for factors
that affect body weight. For simplicity, the causal diagram includes only 3 of
Figure 6.10
those factors: caloric intake Z which (let us assume) can only affect mortality
through weight loss, exercise L which can affect mortality through pathways
other than weight loss, and genetic traits U which can affect mortality through
other pathways that are also independent of weight loss.
Identifying and interpreting the effect of a treatment A on an outcome
Y requires knowledge about how to intervene on A. When there are several
potential ways to intervene on A and some of those potential interventions
have direct effects on the outcome Y as in Figure 6.10, it becomes unclear
what “the effect of A on Y ” means. In our example, reducing weight via
caloric restriction Z would result in a different risk of mortality than reducing
weight via increased exercise L or via genetic manipulation U . Even if one
were willing to disregard the ill-defined causal effect, identifying the variables
needed to achieve exchangeability would be a formidable challenge, as discussed
in Chapter 3.
Being explicit about the interventions of interest is an important step to-
wards having a well-defined causal effect, identifying relevant data, and choos-
ing adjustment variables.
6.5 A structural classification of bias 81
Fine Point 6.3
Discovery of causal structure. In this book we use causal diagrams as a way to represent our expert knowledge—or
assumptions—about the causal structure of the problem at hand. That is, the causal diagram guides the data analysis.
How about going in the opposite direction? Can we learn the causal structure by conducting data analyses without
making assumptions about the causal structure? The process of learning components of the causal structure through
data analysis is referred to as discovery. See the books by Spirtes et al. (2000) and by Peters et al. (2017) for
descriptions of approaches to causal discovery.
We now briefly discuss causal discovery under the assumption that the observed data arose from an unknown causal
DAG that includes, in addition to the observed variables, an unknown number of unobserved variables U. Causal discovery
is sometimes possible if we assume faithfulness, so that statistical independencies in the observed data distribution imply
missing causal arrows on the DAG. Even assuming faithfulness, discovery is often impossible. For example, suppose
that we find a strong association between two variables B and C in our data. We cannot learn the causal structure
involving B and C because their association is consistent with many causal diagrams: B causes C (B → C), C causes
B, (C → B), B and C share an unmeasured cause U (B ←− U → C), B and C have an unobserved common effect
U that has been conditioned on, and various combinations. If we knew the time sequence of B and C, we could only
rule out causal diagrams with either B → C (if C predates B) or C → B (if B predates C ).
There are, however, some settings in which learning causal structure from data appears possible. For example, consider
3 variables Z, A, Y and we know that their time sequence is Z first, A second, and Y last. In the absence of prior
knowledge and empirical data, Figure 6.11 represents a potential causal DAG as we cannot rule out that Z has a direct
effect on A and Y , that A has an effect on Y , or that there exists an unmeasured common cause between any pair of
variables. We also cannot rule out any subgraph with one or more arrows removed.
Now suppose, hypothetically, that data on variables Z, A, and Y become available for an infinite number of individuals.
Our data analysis finds that all 3 variables are marginally associated with each other, and that the only conditional
independence that holds is Z⊥⊥Y |A. Then, if we are willing to assume that faithfulness holds, the only possible causal
DAG consistent with our analysis is Z → A → Y with perhaps a common cause U
1
of Z and A in addition to (or in
place of) the arrow from Z to A. This is because, if either Z was a parent of Y or shared a cause U
2
with Y , or an
unmeasured common cause U
3
of A and Y was present, then Z and Y could not have been statistically independent
given A (assuming faithfulness). Thus, to explain the marginal dependency of Y and A, there must be a causal arrow
from A to Y . (Note that, if an unmeasured common cause of A and Y existed, no conditional independence would be
found and then, even assuming faithfulness, we could not determine whether A causes Y .)
In summary, the causal DAG learned implies that Z is not a direct cause (parent) of Y , that no unmeasured common
cause of A and Y exists, and that, in fact, the average causal effect of A on Y is identified by E[Y |A = 1] −E[Y |A = 0]
because exchangeability holds. Of course, we do not have an infinite sample size. We postpone a discussion about the
implications of having a finite sample for causal discovery until Technical Point 10.7.
6.5 A structural classification of bias
Figure 6.11
The word “bias” is frequently used by investigators making causal inferences.
There are several related, but technically different, uses of the term “bias” (see
Chapter 10). We say that there is systematic bias when the data are insufficient
to identify—compute—the causal effect even with an infinite sample size. (In
this chapter, due to the assumption of an infinite sample size, bias refers to
systematic bias.) Informally, we often refer to systematic bias as any structural
association between treatment and outcome that does not arise from the causal
effect of treatment on outcome in the population of interest. Because causal
diagrams are helpful to represent different sources of association, we can use
causal diagrams to classify systematic bias according to its source, and thus to
sharpen discussions about bias.
Take the crucial source of bias that we have discussed in previous chapters:
82 Graphical representation of causal effects
lack of exchangeability between the treated and the untreated. For the average
causal effect in the entire population, we say that there is (unconditional) bias
when Pr[Y
a=1
= 1] − Pr[Y
a=0
= 1] = Pr[Y = 1|A = 1] − Pr [Y = 1|A = 0],
which is the case when (unconditional) exchangeability Y
a
⊥⊥A does not hold.
Absence of (unconditional) bias implies that the association measure (e.g.,
associational risk ratio or difference) in the population is a consistent estimateWhen there is systematic bias, no
estimator can be consistent. Re-
view Chapter 1 for a definition of
consistent estimator.
of the corresponding effect measure (e.g., causal risk ratio or difference) in the
population.
Lack of exchangeability results in bias even when the null hypothesis of no
causal effect of treatment on the outcome holds. That is, even if the treatment
had no causal effect on the outcome, treatment and outcome would be associ-
ated in the data. We then say that lack of exchangeability leads to bias under
the null. In the observational study summarized in Table 3.1, there was bias
under the null because the causal risk ratio was 1 whereas the associational
risk ratio was 1.26. Any causal structure that results in bias under the nullFor example, conditioning on some
variables may cause selection bias
under the alternative (i.e., off the
null) but not under the null, as de-
scribed by Greenland (1977) and
Hern´an (2017). See also Chapter
18.
will also cause bias under the alternative (i.e., when treatment does have a
non-null effect on the outcome). However, the converse is not true.
For the average causal effects within levels of L, we say that there is con-
ditional bias whenever Pr[Y
a=1
= 1|L = l] − Pr[Y
a=0
= 1|L = l] differs from
Pr[Y = 1|L = l, A = 1] − Pr[Y = 1|L = l, A = 0] for at least one stratum
l, which is generally the case when conditional exchangeability Y
a
⊥⊥A|L = l
does not hold for all a and l.
So far in this book we have referred to lack of exchangeability multiple
times. However, we have yet to explore the causal structures that generate
lack of exchangeability. With causal diagrams added to our methodological
arsenal, we will be able to describe how lack of exchangeability can result from
two different causal structures:
1. Common causes: When the treatment and outcome share a common
cause, the association measure generally differs from the effect measure.
Many epidemiologists use the term confounding to refer to this bias.
2. Conditioning on common effects: This structure is the source of bias that
many epidemiologists refer to as selection bias under the null.
Chapter 7 will focus on confounding bias due to the presence of common
causes, and Chapter 8 on selection bias due to conditioning on common effects.
Again, both are examples of bias under the null due to lack of exchangeability.
Chapter 9 will focus on another source of bias: measurement error. So far
we have assumed that all variables—treatment A , outcome Y , and covariates
L— are perfectly measured. In practice, however, some degree of measurement
error is expected. The bias due to measurement error is referred to as mea-
surement bias or information bias. As we will see, some types of measurement
bias also cause bias under the null.Another form of bias may also re-
sult from (nonstructural) random
variability. See Chapter 10.
Therefore, in the next three chapters we turn our attention to the three
types of systematic bias—confounding, selection, and measurement. These bi-
ases may arise both in observational studies and in randomized experiments.
The susceptibility to bias of randomized experiments may not be obvious from
previous chapters, in which we conceptualized observational studies as some
sort of imperfect randomized experiments, while only considering ideal random-
ized experiments with no participants lost during the follow-up, all participants
adhering to their assigned treatment, and unknown treatment assignment for
both study participants and investigators. While our quasi-mythological char-
acterization of randomized experiments was helpful for teaching purposes, real
6.6 The structure of effect modification 83
randomized experiments rarely look like that. The remaining chapters of Part
I will elaborate on the sometimes fuzzy boundary between experimenting and
observing.
Before that, we take a brief detour to describe causal diagrams in the
presence of effect modification.
6.6 The structure of effect modification
Identifying potential sources of bias is a key use of causal diagrams: we can
use our causal expert knowledge to draw graphs and then search for sources of
association between treatment and outcome. Causal diagrams are less helpful
to illustrate the concept of effect modification that we discussed in Chapter 4.
Figure 6.12
Suppose heart transplant A was randomly assigned in an experiment to
identify the average causal effect of A on death Y . For simplicity, let us
assume that there is no bias, and thus Figure 6.2 adequately represents this
study. Computing the effect of A on the risk of Y presents no challenge.
Because association is causation, the associational risk difference Pr[Y = 1|A =
1]−Pr [Y = 1|A = 0] can be interpreted as the causal risk difference Pr[Y
a=1
=
1]−Pr[Y
a=0
= 1]. The investigators, however, want to go further because they
suspect that the causal effect of heart transplant varies by the quality of medical
care offered in each hospital participating in the study. Thus, the investigators
classify all individuals as receiving high (V = 1) or normal (V = 0) quality of
care, compute the stratified risk differences in each level of V as described in
Chapter 4, and indeed confirm that there is effect modification by V on the
additive scale. The causal diagram in Figure 6.12 includes the effect modifier
V with an arrow into the outcome Y but no arrow into treatment A (which is
randomly assigned and thus independent of V ). Two important caveats.
Figure 6.13
Figure 6.14
Figure 6.15
First, the causal diagram in Figure 6.12 would still be a valid causal diagram
if it did not include V because V is not a common cause of A and Y . It is
only because the causal question makes reference to V (i.e., what is the average
causal effect of A on Y within levels of V ?), that V needs to be included on the
causal diagram. Other variables measured along the path between “quality of
care” V and the outcome Y could also qualify as effect modifiers. For example,
Figure 6.13 shows the effect modifier “therapy complications” N , which partly
mediates the effect of V on Y .
Second, the causal diagram in Figure 6.12 does not necessarily indicate the
presence of effect modification by V . The causal diagram implies that both A
and V affect death Y , but it does not distinguish among the following three
qualitatively distinct ways that V could modify the effect of A on Y :
1. The causal effect of treatment A on mortality Y is in the same direction
(i.e., harmful or beneficial) in both stratum V = 1 and stratum V = 0.
2. The direction of the causal effect of treatment A on mortality Y in stra-
tum V = 1 is the opposite of that in stratum V = 0 (i.e., there is
qualitative effect modification).
3. Treatment A has a causal effect on Y in one stratum of V but no causal
effect in the other stratum A only kills individuals with V = 0.
That is, valid causal graphs such as Figure 6.12 fail to distinguish between
the above three different qualitative types of effect modification by V .
84 Graphical representation of causal effects
In the above example, the effect modifier V had a causal effect on the
outcome. Many effect modifiers, however, do not have a causal effect on the
Figure 6.16
outcome. Rather, they are surrogates for variables that have a causal effect
on the outcome. Figure 6.14 includes the variable “cost of the treatment” S
(1: high, 0: low), which is affected by “quality of care” V but has itself no
effect on mortality Y . An analysis stratified by S (but not by V ) will generally
detect effect modification by S even though the variable that truly modifies
the effect of A on Y is V . The variable S is a surrogate effect modifier whereas
the variable V is a causal effect modifier (see Section 4.2). Because causal and
surrogate effect modifiers are often indistinguishable in practice, the concept
of effect modification comprises both. As discussed in Section 4.2, some prefer
to use the neutral term “heterogeneity of causal effects,” rather than “effect
modification,” to avoid confusion. For example, someone might be tempted
to interpret the statement “cost modifies the effect of heart transplant onFor a finer classification of ef-
fect modification via causal di-
agrams, see VanderWeele and
Robins (2007b)
mortality because the effect is more beneficial when the cost is higher” as an
argument to increase the price of medical care without necessarily increasing
its quality.
A surrogate effect modifier is simply a variable associated with the causal
effect modifier. Figure 6.14 depicts the setting in which such association is
due to the effect of the causal effect modifier on the surrogate effect modifier.
However, such association may also be due to shared common causes or con-
ditioning on common effects. For example, Figure 6.15 includes the variables
“place of residence” (1: Greece, 0: Rome) U and “passport-defined national-
ity” P (1: Greece, 0: Rome). Place of residence U is a common cause of both
quality of care V and nationality P . Thus P will behave as a surrogate effect
modifier because P is associated with the causal effect modifier V . Another
(admittedly silly) example to illustrate this issue: Figure 6.16 includes the
variables “cost of care” S and “use of bottled mineral water (rather than tap
water) for drinking at the hospital” W . Use of mineral water W affects cost
S but not mortality Y in developed countries. If the study were restricted to
low-cost hospitals (S = 0), then use of mineral water W would be generallySome intuition for the association
between W and V in low-cost hos-
pitals S = 0: suppose that low-
cost hospitals that use mineral wa-
ter need to offset the extra cost of
mineral water by spending less on
components of medical care that
decrease mortality. Then use of
mineral water would be inversely
associated with quality of medical
care in low-cost hospitals.
associated with medical care V , and thus W would behave as a surrogate effect
modifier. In summary, surrogate effect modifiers can be associated with the
causal effect modifier by structures including common causes, conditioning on
common effects, or cause and effect.
Causal diagrams are in principle agnostic about the presence of interaction
between two treatments A and E. However, causal diagrams can encode infor-
mation about interaction when augmented with nodes that represent sufficient-
component causes (see Chapter 5), i.e., nodes with deterministic arrows from
the treatments to the sufficient-component causes. Because the presence of
interaction affects the magnitude and direction of the association due to con-
ditioning on common effects, these augmented causal diagrams are discussed
in Chapter 8.
Chapter 7
CONFOUNDING
Suppose an investigator conducted an observational study to answer the causal question “does one’s looking up to
the sky make other pedestrians look up too?” She found an association between a first pedestrian’s looking up and
a second one’s looking up. However, she also found that pedestrians tend to look up when they hear a thunderous
noise above. Thus it was unclear what was making the second pedestrian look up, the first pedestrian’s looking
up or the thunderous noise? She concluded the effect of one’s looking up was confounded by the presence of a
thunderous noise.
In randomized experiments treatment is assigned by the flip of a coin, but in observational studies treatment
(e.g., a person’s looking up) may be determined by many factors (e.g., a thunderous noise). If those factors affect
the risk of developing the outcome (e.g., another person’s looking up), then the effects of those factors become
entangled with the effect of treatment. We then say that there is confounding, which is just a form of lack of
exchangeability between the treated and the untreated. Confounding is often viewed as the main shortcoming of
observational studies. In the presence of confounding, the old adage “association is not causation” holds even if the
study population is arbitrarily large. This chapter provides a definition of confounding and reviews the methods
to adjust for it.
7.1 The structure of confounding
The structure of confounding, the bias due to common causes of treatment
and outcome, can be represented by using causal diagrams. For example, the
Figure 7.1
diagram in Figure 7.1 (same as Figure 6.1) depicts a treatment A, an outcome
Y , and their shared (or common) cause L. This diagram shows two sources
of association between treatment and outcome: 1) the path A → Y that
represents the causal effect of A on Y , and 2) the path A ← L → Y between
A and Y that includes the common cause L. The path A ← L → Y that links
A and Y through their common cause L is an example of a backdoor path.
If the common cause L did not exist in Figure 7.1, then the only path
between treatment and outcome would be A → Y , and thus the entire asso-In a causal DAG, a backdoor path
is a noncausal path between treat-
ment and outcome that remains
even if all arrows pointing from
treatment to other variables (the
descendants of treatment) are re-
moved. That is, the path has an
arrow pointing into treatment.
ciation between A and Y would be due to the causal effect of A on Y . That
is, the associational risk ratio Pr [Y = 1|A = 1] / Pr [Y = 1|A = 0] would equal
the causal risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
; association would be cau-
sation. But the presence of the common cause L creates an additional source of
association between the treatment A and the outcome Y , which we refer to as
confounding for the effect of A on Y . Because of confounding, the associational
risk ratio does not equal the causal risk ratio; association is not causation.
Examples of confounding abound in observational research. Consider the
following examples of confounding for the effect of various kinds of treatments
on health outcomes:
• Occupational factors: The effect of working as a firefighter A on the risk
of death Y will be confounded if “being physically fit” L is a cause of
both being an active firefighter and having a lower mortality risk. This
86 Confounding
bias, depicted in the causal diagram in Figure 7.1, is often referred to as
a healthy worker bias.
• Clinical decisions: The effect of drug A (say, aspirin) on the risk of
Figure 7.2
disease Y (say, stroke) will be confounded if the drug is more likely to
be prescribed to individuals with certain condition L (say, heart disease)
that is both an indication for treatment and a risk factor for the disease.
Heart disease L is a risk factor for stroke Y because L has a direct causal
effect on Y as in Figure 7.1 or, as in Figure 7.2, because both L and Y
Some authors prefer to replace the
unmeasured common cause U (and
the two arrows leaving it) by a bidi-
rectional edge between the mea-
sured variables that U causes.
are caused by atherosclerosis U, an unmeasured variable. This bias is
known as confounding by indication or channeling, the last term often
being reserved to describe the bias created by patient-specific risk factors
L that encourage doctors to use certain drug A within a class of drugs.
• Lifestyle: The effect of behavior A (say, exercise) on the risk of Y (say,
death) will be confounded if the behavior is associated with another
behavior L (say, cigarette smoking) that has a causal effect on Y and
tends to co-occur with A. The structure of the variables L, A, and Y is
depicted in the causal diagram in Figure 7.3, in which the unmeasured
Figure 7.3
variable U represents the sort of personality and social factors that lead to
both lack of exercise and smoking. Another frequent problem: subclinical
disease U results both in lack of exercise A and an increased risk of
clinical disease Y . This form of confounding is often referred to as reverse
causation when L is unknown.
• Genetic factors: The effect of a DNA sequence A on the risk of developing
certain trait Y will be confounded if there exists a DNA sequence L that
has a causal effect on Y and is more frequent among people carrying A.
This bias, also represented by the causal diagram in Figure 7.3, is known
as linkage disequilibrium or population stratification, the last term often
being reserved to describe the bias arising from conducting studies in a
mixture of individuals from different ethnic groups. Thus the variable
U can stand for ethnicity or other factors that result in linkage of DNA
sequences.
Early statistical descriptions of con-
founding were provided by Yule
(1903) for discrete variables and by
Pearson et al. (1899) for contin-
uous variables. Yule described the
association due to confounding as
“fictitious”, “illusory”, and “appar-
ent”. Pearson et al. (1899) re-
ferred to it as a “spurious” corre-
lation. However, there is nothing
fictitious, illusory, apparent, or spu-
rious about these associations. As-
sociations due to common causes
are quite real associations, though
they cannot be causally interpreted
as treatment effects. Or, in Yule’s
words, they are associations “to
which the most obvious physical
meaning must not be assigned.”
• Social factors: The effect of income at age 65 A on the level of disability
at age 75 Y will be confounded if the level of disability at age 55 L affects
both future income and disability level. This bias may be depicted by
the causal diagram in Figure 7.1.
• Environmental exposures: The effect of airborne particulate matter A on
the risk of coronary heart disease Y will be confounded if other pollutants
L whose levels co-vary with those of A cause coronary heart disease. This
bias is also represented by the causal diagram in Figure 7.3, in which the
unmeasured variable U represent weather conditions that affect the levels
of all types of air pollution.
In all these cases, the bias has the same structure: it is due to the pres-
ence of a cause (L or U) that is shared by the treatment A and the outcome
Y , which results in an open backdoor path between A and Y . We refer to
the bias caused by shared causes of treatment and outcome as confounding,
and we use other names to refer to biases caused by structural reasons other
than the presence of shared causes of treatment and outcome. For simplicity
of presentation, we assume throughout this chapter that positivity and consis-
tency hold, that all nodes in the causal diagrams are perfectly measured, that
7.2 Confounding and exchangeability 87
there are no selection nodes S with a box around them (that is, the data are a
random sample from the population of interest), and that random variability
is absent. Causal diagrams with selection nodes will be discussed in Chap-
ter 8, and causal diagrams with mismeasured nodes in Chapter 9. Random
variability is discussed in Chapter 10.
7.2 Confounding and exchangeability
We now link the concept of confounding, which we have defined using causal
diagrams, with the concept of exchangeability, which we have defined usingSee Greenland and Robins (1986,
2009) for a detailed discussion on
the relations between confounding
and exchangeability.
counterfactuals in earlier chapters.
When exchangeability Y
a
⊥⊥A holds, as in a marginally randomized experi-
ment in which all individuals have the same probability of receiving treatment,
the average causal effect can be identified without adjustment for any vari-
ables. For a binary treatment A, the average causal effect E[Y
a=1
] − E[Y
a=0
]
is calculated as the difference of conditional means E[Y |A = 1] − E[Y |A = 0].
When exchangeability Y
a
⊥⊥A does not hold but conditional exchangeabil-
ity Y
a
⊥⊥A|L does, as in a conditionally randomized experiment in which the
probability of receiving treatment varies across values of L, the average causal
effect can also be identified. However, as we described in Chapter 2, iden-
tification of the causal effect E[Y
a=1
] − E[Y
a=0
] in the population requires
adjustment for the variables L via standardization or IP weighting. Also, asUnder conditional exchangeability,
E[Y
a=1
] − E[Y
a=0
] =
P
l
E[Y |L = l, A = 1] Pr [L = l] −
P
l
E[Y |L = l, A = 0] Pr [L = l].
we described in Chapter 4, conditional exchangeability also allows the identifi-
cation of the conditional causal effects E[Y
a=1
|L = l] − E[Y
a=0
|L = l] for any
value l via stratification.
In practice, if we believe confounding is likely, a key question arises: can
we determine whether there exists a set of measured covariates L for which
conditional exchangeability holds? Answering this question is difficult because
thinking in terms of conditional exchangeability Y
a
⊥⊥A|L is often not intuitive
in complex causal systems.
In this chapter, we will see that answering this question is possible if one
knows the causal DAG that generated the data. To do so, suppose that we
know the true causal DAG (for now, it doesn’t matter how we know it: perhaps
we have sufficient subject-matter knowledge, or perhaps an omniscient god gave
it to us). How does the causal DAG allow us to determine whether there exists
a set of variables L for which conditional exchangeability holds? There are
two main approaches: (i) the backdoor criterion applied to the causal DAGPearl (1995, 2009) proposed the
backdoor criterion for nonparamet-
ric identification of causal effects.
and (ii) the transformation of the causal DAG into a SWIG. Though the use
of SWIGs is a more direct approach, it also requires a bit more machinery so
we are going to first explain the backdoor criterion; we will describe the SWIG
approach in Section 7.5.
A set of covariates L satisfies the backdoor criterion if all backdoor paths
between A and Y are blocked by conditioning on L and L contains no variables
that are descendants of treatment A. Under faithfulness and a further condition
discussed in Technical Point 7.1, conditional exchangeability Y
a
⊥⊥A|L holds if
and only if L satisfies the backdoor criterion. (A simple proof of this fact will
be given below based on SWIGs.) Hence, we can now answer any query we may
have about whether, for a given set of covariates L, conditional exchangeability
given L holds. Thus, by trying every subset of measured non-descendants of
treatment, we can answer the question of whether conditional exchangeability
holds for any subset. (In fact, algorithms exist that can greatly reduce the
88 Confounding
Technical Point 7.1
Does conditional exchangeability imply the backdoor criterion? That L satisfies the backdoor criterion always
implies conditional exchangeability given L, even in the absence of faithfulness. In the main text we also said that,
given faithfulness, conditional exchangeability given L implies that L satisfies the backdoor criterion. This last sentence
is true under an FFRCISTG model (see Technical Point 6.2). In contrast, under an NPSEM-IE model, conditional
exchangeability can hold even if the backdoor criterion does not, as is the case in a causal DAG with nodes A, L, Y and
arrows A → L, A → Y . In this book we always assume an FFRCISTG model and faithfulness, unless stated otherwise.
This difference between causal models is due to the fact that the NPSEM-IE, unlike an FFRCISTG model, assumes
cross-world independencies between counterfactuals. However a cross-world independence can never be verified, even in
principle, by any randomized experiment, which was the very reason that Robins (1986, 1987) did not assume cross-world
independencies in his FFRCISTG model. We will return to this issue in Chapter 23.
number of subsets that must be tried in order to answer the question.)
Let us now relate the backdoor criterion (i.e., exchangeability) to confound-
ing. The two settings in which the backdoor criterion is satisfied are
1. No common causes of treatment and outcome. In Figure 6.2, there are
no common causes of treatment and outcome, and hence no backdoor
paths that need to be blocked. Then the set of variables that satisfies
the backdoor criterion is the empty set and we say that there is no con-
founding.
2. Common causes of treatment and outcome but a subset L of measured
non-descendants of A suffices to block all backdoor paths. In Figure 7.1,
the set of variables that satisfies the backdoor criterion is L. Thus, we
say that there is confounding, but that there is no residual confounding
whose elimination would require adjustment for unmeasured variables
(which, of course, is not possible). For brevity, we say that there is no
unmeasured confounding.
The first setting describes a marginally randomized experiment in which
confounding is not expected because treatment assignment is solely deter-
mined by the flip of a coin—or its computerized upgrade: the random number
generator—and the flip of the coin cannot cause the outcome. That is, when the
treatment is unconditionally randomly assigned, the treated and the untreated
are expected to be exchangeable because no common causes exist or, equiva-
lently, because there are no open backdoor paths. Marginal exchangeability,
i.e., Y
a
⊥⊥A, is equivalent to no common causes of treatment and outcome.
The second setting describes a conditionally randomized experiment in
which the probability of receiving treatment is the same for all individuals
with the same value of L but, by design, this probability varies across values
of L, that is there is an arrow L → A. This experimental design guarantees
confounding if L is also either a cause of the outcome (as in Figure 7.1) or the
descendant of an unmeasured cause of the outcome as in Figure 7.2. Hence,
there are open backdoor paths. However, conditioning on the covariates L
will block all backdoor paths and therefore conditional exchangeability, i.e.,
Y
a
⊥⊥A|L, will hold. We say that a set L of measured non-descendants of A
is a sufficient set for confounding adjustment when conditioning on L blocks
all backdoor paths—that is, the treated and the untreated are exchangeable
within levels of L.
7.3 Confounding and the backdoor criterion 89
Take our heart transplant study, a conditionally randomized experiment,
as an example. Individuals who received a transplant (A = 1) are different
from the others (A = 0) because, had the treated remained untreated, their
risk of death Y would have been higher than that of those that were actually
untreated—the treated had a higher frequency of severe heart disease L, a
common cause of A and Y . The presence of common causes of treatment
and outcome implies that the treated and the untreated are not marginally
exchangeable but are conditionally exchangeable given L. This second setting
is also what one hopes for in observational studies in which many variables L
have been measured.
The backdoor criterion does not answer questions regarding the magnitude
or direction of confounding. It is logically possible that some unblocked back-
door paths are weak (e.g., if L does not have a large effect on either A or Y )
and thus induce little bias, or that several strong backdoor paths induce bias
in opposite directions and thus result in a weak net bias. Because unmeasured
confounding is not an “all or nothing” issue, in practice, it is important to
consider the expected direction and magnitude of the bias (see Fine Point 7.1).
7.3 Confounding and the backdoor criterion
We now describe several examples of the application of the backdoor criterion
to determine whether the causal effect of A on Y is identifiable and, if so, which
variables are required to ensure conditional exchangeability. Remember that
all causal DAGs in this chapter include perfectly measured nodes that are not
conditioned on.
In Figure 7.1 there is confounding because the treatment A and the outcome
Y share the cause L, i.e., because there is an open backdoor path between A
and Y through L. However, this backdoor path can be blocked by conditioning
on L. Thus, if the investigators collected data on L for all individuals, there
is no unmeasured confounding given L.
In Figure 7.2 there is confounding because the treatment A and the outcome
Y share the unmeasured cause U, i.e., there is a backdoor path between A and
Y through U . (Unlike the variables L, A, and Y , the variable U was not
measured by the investigators.) This backdoor path could be theoretically
blocked, and thus confounding eliminated, by conditioning on U, had data on
this variable been collected. However, this backdoor path can also be blocked
Figure 7.4 by conditioning on L. Thus, there is no unmeasured confounding given L.
In Figure 7.3 there is also confounding because the treatment A and the
outcome Y share the cause U , and the backdoor path can also be blocked by
conditioning on L. Therefore there is no unmeasured confounding given L.
Now consider Figure 7.4. In this causal diagram there are no common
causes of treatment A and outcome Y , and therefore there is no confounding.
The backdoor path between A and Y through L (A ← U
2
→ L ← U
1
→
Y ) is blocked because L is a collider on that path. Thus all the association
between A and Y is due to the effect of A on Y : association is causation. For
example, suppose A represents physical activity, Y cervical cancer, U
1
a pre-
cancer lesion, L a diagnostic test (Pap smear) for pre-cancer, and U
2
a health-
conscious personality (more physically active, more visits to the doctor). Then,
under the causal diagram in Figure 7.4, the effect of physical activity A on
cancer Y is unconfounded and there is no need to adjust for L to compute either
Pr[Y
a=1
] or Pr[Y
a=0
] and thus to compute the causal effect in the population.
90 Confounding
Fine Point 7.1
The strength and direction of confounding bias. Suppose you conducted an observational study to identify the effect
of heart transplant A on death Y and that you assumed no unmeasured confounding. A thoughtful critic says “the
inferences from this observational study may be incorrect because of potential confounding due to cigarette smoking
L.” A crucial question is whether the bias results in an attenuated or an exaggerated estimate of the effect of heart
transplant. For example, suppose that the risk ratio from your study was 0.6 (heart transplant was estimated to reduce
mortality during the follow-up by 40%) and that, as the reviewer suspected, cigarette smoking L is a common cause
of A (cigarette smokers are less likely to receive a heart transplant) and Y (cigarette smokers are more likely to die).
Because there are fewer cigarette smokers (L = 1) in the heart transplant group (A = 1) than in the other group
(A = 0), one would have expected to find a lower mortality risk in the group A = 1 even under the null hypothesis of
no effect of treatment A on Y . Adjustment for cigarette smoking will therefore move the effect estimate upwards (say,
from 0.6 to 0.7). In other words, lack of adjustment for cigarette smoking resulted in an exaggeration of the beneficial
average causal effect of heart transplant.
An approach to predict the direction of confounding bias is the use of signed causal diagrams. Consider the causal
diagram in Figure 7.1 with dichotomous L, A, and Y variables. A positive sign over the arrow from L to A is added if
L has a positive average causal effect on A (i.e., if the probability of A = 1 is greater among those with L = 1 than
among those with L = 0), otherwise a negative sign is added if L has a negative average causal effect on A (i.e., if the
probability of A = 1 is greater among those with L = 0 than among those with L = 1). Similarly a positive or negative
sign is added over the arrow from L to Y . If both arrows are positive or both arrows are negative, then the confounding
bias is said to be positive, which implies that effect estimate will be biased upwards in the absence of adjustment for
L. If one arrow is positive and the other one is negative, then the confounding is said to be negative, which implies
that the effect estimate will be biased downwards in the absence of adjustment for L. Unfortunately, this simple rule
may fail in more complex causal diagrams or when the variables are non dichotomous. See VanderWeele, Hern´an, and
Robins (2008) for a more detailed discussion of signed diagrams in the context of average causal effects.
Regardless of the sign of confounding, another key issue is the magnitude of the bias. Biases that are not large enough
to affect the conclusions of the study may be safely ignored in practice, whether the bias is upwards or downwards. A
large confounding bias requires a strong confounder-treatment association and a strong confounder-outcome association
(conditional on the treatment). For discrete confounders, the magnitude of the bias depends also on prevalence of
the confounder (Cornfield et al. 1959, Walker 1991). If the confounders are unknown, one can only guess what the
magnitude of the bias is. Educated guesses can be organized by conducting sensitivity analyses (i.e., repeating the
analyses under several assumptions regarding the magnitude of the bias), which may help quantify the maximum bias
that is reasonably expected. See Rosenbaum (2005), Greenland (1996a), Robins, Rotnitzky, and Scharfstein (1999),
Greenland and Lash (2008), and VanderWeele and Arah (2011) for detailed descriptions of sensitivity analyses for
unmeasured confounding.
Suppose, as in the last four examples, that data on L, A, and Y suffice to
identify the causal effect. In such setting we define L to be a confounder ifAn informal definition for Figures
7.1 to 7.4: ‘A confounder is any
variable that can be used to adjust
for confounding.’ Note this defini-
tion is not circular because we have
previously provided a definition of
confounding. Another example of
a non-circular definition: “A musi-
cian is a person who plays music,”
stated after we have defined what
music is.
the data on A and Y do not suffice for identification (i.e., we have structural
confounding). We define L to be a non-confounder if data on A, Y alone suffice
for identification. These definitions are equivalent to defining L as a confounder
if there is conditional exchangeability but not unconditional exchangeability
(i.e., structural confounding) and as a non-confounder if there is unconditional
exchangeability.
Thus, in Figures 7.1-7.3, L is a confounder because Pr[Y
a
= 1] is identified
by the standardized risk
P
l
Pr [Y = 1|A = a, L = l] Pr [L = l]. In Figures 7.2
and 7.3, L is not a common cause of A and Y , yet we still say that L is a
confounder because it is needed to block the open backdoor path attributable
to the unmeasured common cause U of A and Y . In Figure 7.4, L is a non-
confounder and the identifying formula for Pr[Y
a
= 1] is just the conditional
7.3 Confounding and the backdoor criterion 91
mean Pr[Y = 1|A = a].
Interestingly, in Figure 7.4, conditional exchangeability given L does notThe possibility of identification of
unconditional effects without iden-
tification of conditional effects was
non-graphically demonstrated by
Greenland and Robins (1986). The
conditional bias in Figure 7.4 was
described by Greenland, Pearl, and
Robins (1999) and referred to as M-
bias (Greenland 2003) because the
structure of the variables involved
in it—U
2
, L, U
1
—resembles a letter
M lying on its side.
hold and thus the counterfactual risks Pr[Y
a
= 1|L = l] are not equal to
the stratum-specific risks Pr[Y = 1|A = a, L = l], and the conditional treat-
ment effects with strata of L are not identified. Further, adjustment for L via
standardization
P
l
Pr [Y = 1|A = a, L = l] Pr [L = l] gives a biased estimate
of Pr[Y
a
]. This follows from the fact that adjustment for L would induce bias
because conditioning on the collider L opens the backdoor path between A
and Y (A ← U
2
→ L ← U
1
→ Y ), which was previously blocked by the col-
lider itself. Thus the association between A and Y would be a mixture of the
association due to the effect of A on Y and the association due to the open
backdoor path. Association would not be causation any more. This is the first
example we have seen for which unconditional exchangeability holds but con-
ditional exchangeability does not: the average causal effect is identified, but
generally not the conditional causal effects within levels of L. We refer to theIf U
1
caused U
2
, or U
2
caused U
1
,
or an unmeasured U
3
caused both,
there would exist a common cause
of A and Y , and we would have nei-
ther unconditional nor conditional
exchangeability given L.
resulting bias in the conditional effect as selection bias because it it arises from
selecting (conditioning) on the common effect L of two marginally independent
variables U
1
and U
2
, one of which is associated with A and the other with Y
(see Chapter 8).
The causal diagram in Figure 7.5 is a variation of the one in Figure 7.4.
The difference is that, in Figure 7.5, there is an arrow L → A. The presence
of this arrow creates an open backdoor path A ← L ← U
1
→ Y because U
1
is a common cause of A and Y , and so confounding exists. Conditioning onThe definition of collider is path-
specific: L is a collider on the path
A ← U
2
→ L ← U
1
→ Y , but not
on the path A ← L ← U
1
→ Y .
L would block that backdoor path but would simultaneously open a backdoor
path on which L is a collider (A ← U
2
→ L ← U
1
→ Y ).
Figure 7.5
Therefore, in Figure 7.5, the bias is intractable: attempting to block the
confounding path opens a selection bias path. There is neither unconditional
exchangeability nor conditional exchangeability given L. A solution to the bias
in Figure 7.5 would be to measure either (i) a variable L
1
between U
1
and either
A or Y , or (ii) a variable L
2
between U
2
and either A or L. In the first case we
would have conditional exchangeability given L
1
. In the second case we would
have conditional exchangeability given both L
2
and L. For example, Figure
7.6 includes the variable L
1
between U
1
and Y and the variable L
2
between
Figure 7.6
U
2
and A. See Fine Point 7.2 for a discussion of identification of causal effects
depending on what variables are measured in Figure 7.6.
The causal diagrams in this section depict two structural sources of lack of
exchangeability that are due to the presence of open backdoor paths between
treatment and outcome. The first source is the presence of common causes
of treatment and outcome—which creates an open backdoor path. The sec-
ond source is conditioning on a common effect—which may open a previously
blocked backdoor path. For pedagogic purposes, we have reserved the term
“confounding” for the first and “selection bias” for the latter. An alterna-
tive way to structurally define confounding could be the “bias due to an open
backdoor path between A and Y .” This alternative definition is identical to
ours except that it labels the bias due to conditioning on L in Figure 7.4 as
confounding rather than as selection bias. The alternative definition can be
equivalently expressed as follows: confounding is “any systematic bias that
would be eliminated by randomized assignment of A”. To see this, note that
the bias induced in Figure 7.4 by conditioning on L could not occur in an
experiment in which treatment A is randomly assigned because the random
assignment ensures the absence of an unmeasured U
2
that is a common cause
of A and L and thus conditioning on L would no longer open a backdoor path.
One interesting distinction between these two definitions is the following.
92 Confounding
Fine Point 7.2
Identification of conditional and unconditional effects. Under any causal diagram, the causal effects that can be
identified depend on the variables that are measured in addition to the treatment and the outcome. Take Figure 7.6 as
an example. If we measure only L
2
(but not L and L
1
), we have neither unconditional nor conditional exchangeability
given L
2
, and no causal effects can be identified. If we measure L
2
and L, we have conditional exchangeability given
L
2
and L, but we do not have conditional exchangeability given either L
2
alone or L alone. However, we can identify:
• The conditional causal effects within joint strata of L
2
and L. The identifying formula for each of the counterfactual
means is E [Y |A = a, L = l, L
2
= l
2
].
• The unconditional causal effect. The identifying formula for each of the counterfactual means is
P
l,l
2
E [Y |A = a, L = l, L
2
= l
2
] Pr [L = l, L
2
= l
2
].
• The conditional causal effects within strata of L. The identifying formula for each of the counterfactual means is
P
l
2
E [Y |A = a, L = l, L
2
= l
2
] Pr [L
2
= l
2
|L = l].
• The conditional causal effects within strata of L
2
. The identifying formula for each of the counterfactual means
is
P
l
E [Y |A = a, L = l, L
2
= l
2
] Pr [L = l|L
2
= l
2
].
If we only measure L
1
, then we have conditional exchangeability given L
1
so we can identify the conditional causal
effects within strata of L
1
and the unconditional causal effect. If we measure L
1
and L, then we can also identify the
conditional causal effects within joint strata of L
1
and L, and within strata of L alone. If we measure L, L
1
, and L
2
,
then we can also identify the conditional effects within joint strata of all three variables.
The existence of a common cause of treatment and the outcome (the structural
definition of confounding) is a substantive fact about the study population
and the world, independent of the method chosen to analyze the data. On
the other hand, the definition of confounding as any bias that would have been
eliminated by randomization implies that the existence of confounding depends
on the method of analysis. In Figure 7.4, we have no confounding if we do not
adjust for L, but we introduce confounding if we do adjust.
Nonetheless, the choice of one definition over the other is just a matter of
taste with no practical implications as all our conclusions regarding identifia-
bility are based solely on whether conditional or unconditional exchangeability
holds and not on our definition of confounding. The next chapter provides
more detail on the distinction between confounding and selection bias.
7.4 Confounding and confounders
In the previous section, we have described how to use causal diagrams to
decide whether confounding exists and, if so, to identify whether a given set
of measured variables L is a sufficient set for confounding adjustment. The
procedure requires a priori knowledge of the causal DAG that includes all
causes—both measured and unmeasured—shared by the treatment A and the
outcome Y . Once the causal diagram is known, we simply need to apply the
backdoor criterion to determine what variables need to be adjusted for.
In contrast, the traditional approach to handle confounding was based
mostly on observed associations rather than on prior causal knowledge. The
traditional approach first labels variables that meet certain (mostly) associa-
7.4 Confounding and confounders 93
tional conditions as confounders and then mandates that these so-called con-
founders are adjusted for in the analysis. Confounding is said to exist whenTechnically, investigators do not
need structural knowledge. They
only need to know a set of vari-
ables that guarantees conditional
exchangeability.
the adjusted estimate differs from the unadjusted estimate.
Under the traditional approach, a confounder was defined as a variable that
meets the following three conditions: (1) it is associated with the treatment,
(2) it is associated with the outcome conditional on the treatment (with “con-
ditional on the treatment” often replaced by “in the untreated”), and (3) it
does not lie on a causal pathway between treatment and outcome. However,
this traditional approach may lead to inappropriate adjustment. To see why,
let us revisit Figures 7.1-7.4.
In Figure 7.1, the variable L is associated with the treatment (because it
has a causal effect on A), is associated with the outcome conditional on the
treatment (because it has a direct causal effect on Y ), and it does not lie
on the causal pathway between treatment and outcome. In Figure 7.2, the
variable L is associated with the treatment (because it has a causal effect on
A), is associated with the outcome conditional on the treatment (because it
shares the cause U with Y ), and it does not lie on the causal pathway between
treatment and outcome. In Figure 7.3, L is associated with the treatment (it
shares the cause U with A), is associated with the outcome conditional on
the treatment (it has a causal effect on Y ), and it does not lie on the causal
pathway between treatment and outcome.
Therefore, according to the traditional approach, L is a confounder in the
settings represented by Figures 7.1-7.3 and it needs be adjusted for. That was
also our conclusion when using the backdoor criterion in the previous section.
For Figures 7.1-7.3, there is no discrepancy between the traditional, mostly
associational approach and the application of the backdoor criterion to the
causal diagram.
Now consider Figure 7.4 again in which there is no confounding and L is a
non-confounder by the definition given in Section 7.3. However, L meets the
criteria for a traditional confounder: it is associated with the treatment (it
shares the cause U
2
with A), it is associated with the outcome conditional on
the treatment (it shares the cause U
1
with Y ), and it does not lie on the causal
pathway between treatment and outcome. Hence, according to the traditional
Figure 7.7
approach, L is a confounder that should be adjusted for, even in the absence
of confounding! But, as we saw above, adjustment for L results in a biased
estimator of the causal effect in the population due to selection bias. Figure
7.7 is another example in which the traditional approach leads to inappropriate
adjustment for L by inducing selection bias.
Figure 7.8
These examples show that associational or statistical criteria are insufficient
to characterize confounding. An approach based on a definition of confounder
that relies almost exclusively on statistical considerations may lead, as shown
by Figures 7.4 and 7.7, to the wrong advice: adjust for a “confounder” even
when structural confounding does not exist. To eliminate this problem for Fig-
ure 7.4, a follower of the traditional approach might replace the associational
condition “(2) it is associated with the outcome conditional on the treatment”
by the structural condition “(2) it is a cause of the outcome.” This modified def-
inition of confounder prevents inappropriate adjustment for L in Figure 7.4,
but only to create a new problem by not considering L a confounder—that
needs to be adjusted for—in Figure 7.2. See Technical Point 7.2.
The traditional approach misleads investigators into adjusting for variables
when adjustment is harmful. The problem arises because the traditional ap-
proach starts by defining confounders in the absence of sufficient causal knowl-
edge about the sources of confounding, and then mandates adjustment for
94 Confounding
Fine Point 7.3
Surrogate confounders. Under the causal DAG in Figure 7.8, there is confounding for the effect of A on Y because
of the presence of the unmeasured common cause U . The measured variable L is a proxy or surrogate for U. For
example, the unmeasured variable socioeconomic status U may confound the effect of physical activity A on the risk
of cardiovascular disease Y . Income L is a surrogate for the often ill-defined variable socioeconomic status. Should
we adjust for the variable L? On the one hand, it can be said that L is not a confounder because it does not lie on
a backdoor path between A and Y . On the other hand, adjusting for the measured L, which is associated with the
unmeasured U, may indirectly adjust for some of the confounding caused by U . In the extreme, if L were perfectly
correlated with U then it would make no difference whether one conditions on L or on U. Indeed if L is binary and is
a nondifferentially misclassified (see Chapter 9) version of U, conditioning on L will result in a partial blockage of the
backdoor path A ← U → Y under some weak conditions (Greenland 1980, Ogburn and VanderWeele 2012). Therefore
we will typically prefer to adjust, rather than not to adjust, for L.
We refer to variables that can be used to reduce confounding bias even though they are not on a backdoor path (and
so could never completely eliminate confounding) as surrogate confounders. A possible strategy to fight confounding is
to measure as many surrogate confounders as possible and adjust for all of them. See Chapter 18 for discussion.
those so-called confounders. If the adjusted and unadjusted estimates dif-
fer, the traditional approach declares the existence of confounding. However,
change in estimates may occur for reasons other than confounding, including
selection bias when adjusting for non-confounders (see Chapter 8) and the use
of noncollapsible effect measures (see Fine Point 4.3). Attempts to define con-
founding based on change in estimates have been long abandoned because of
these problems.
In contrast, a structural approach starts by explicitly identifying the sources
of confounding—the common causes of treatment and outcome that, were they
all measured, would be sufficient to adjust for confounding—and then identifies
a sufficient set of adjustment variables.
The structural approach makes clear that including a particular variable
in a sufficient set depends on the variables already included in the set. For
example, in Figures 7.2 and 7.3 the set of variables L is needed to block a
backdoor path because the set of variables U is not measured. We could then
say that the variables in L are confounders. However, if the variables U had
been measured and used to block the backdoor path, then the variables L
would not be confounders given U (see also Fine Point 7.3). Given a causal
DAG, confounding is an absolute concept whereas confounder is a relative one.VanderWeele and Shpitser (2013)
also proposed a formal definition of
confounder.
A structural approach to confounding emphasizes that causal inference from
observational data requires a priori causal knowledge. This causal knowledge
is summarized in a causal DAG that encodes the researchers’ beliefs or as-
sumptions about the causal network. Of course, there is no guarantee that the
researchers’ causal DAG is correct and thus it is possible that, contrary to the
researchers’ beliefs, their chosen set of adjustment variables fails to eliminate
confounding or introduces selection bias. However, the structural approach
to confounding has two important advantages. First, it prevents inconsisten-
cies between beliefs and actions. For example, if you believe Figure 7.4 is the
true causal diagram—and therefore that there is no confounding for the effect
of A on Y —then you will not adjust for the variable L, regardless of what
non-structural definitions of confounder may say. Second, the researchers’ as-
sumptions about confounding become explicit and therefore can be explicitly
criticized by other investigators.
7.5 Single-world intervention graphs 95
Technical Point 7.2
Fixing the traditional definition of confounder. Figures 7.4 and 7.7 depict two graphical examples in which the
traditional non-graphical definition of confounder and confounding misleads investigators into adjusting for a variable
when adjustment for such variable is not only superfluous but also harmful. The traditional definition fails because it
relies on two incorrect statistical criteria—conditions (1) and (2)—and one incorrect causal criterion—condition (3). To
“fix” the traditional definition one needs to do two things:
1. Replace condition (3) by the condition that “there exist variables L and U such that there is conditional exchange-
ability within their joint levels Y
a
⊥⊥A|L, U. This new condition is stronger than the earlier condition because it
effectively implies that L is not on a causal pathway between A and Y and that E[Y
a
|L = l, U = u] is identified
by E[Y |L = l, U = u, A = a].
2. Replace conditions (1) and (2) by the following condition: U can be decomposed into two disjoint subsets U
1
and
U
2
(i.e., U = U
1
∪ U
2
and U
1
∩ U
2
is empty) such that (i) U
1
and A are not associated within strata of L, and
(ii) U
2
and Y are not associated within joint strata of A, L, and U
1
. The variables in U
1
may be associated with
the variables in U
2
. U
1
can always be chosen to be the largest subset of U that is unassociated with treatment.
If these two new conditions are met we say U is a non-confounder given data on L. These conditions were proposed
by Robins (1997a, Theorem 4.3) and further discussed by Greenland, Pearl, and Robins (1999, pp. 45-46, note the
condition that U = U
1
∪U
2
was inadvertently left out). These conditions overcome the difficulties found in Figures 7.4
and 7.7 because they allow us to dismiss variables as non-confounders (Robins 1997a). For example, Greenland, Pearl,
and Robins applied these conditions to Figure 7.4 to show that there is no confounding.
7.5 Single-world intervention graphs
Exchangeability is translated into graph language as the lack of open paths
between the treatment A and outcome Y nodes—other than those originating
from A—that would result in an association between A and Y . Chapters 7–
9 describe different ways in which lack of exchangeability can be represented
in causal diagrams. For example, in this chapter we discuss confounding, a
violation of exchangeability due to the presence of an open backdoor path
between treatment and outcome.
The equivalence between unconditional exchangeability Y
a
⊥⊥A and the
backdoor criterion seems rather magical: there appears to be no obvious re-
lationship between counterfactual independence and the absence of backdoor
paths because counterfactuals are not included as variables on causal diagrams.
Since graphs are so useful for evaluating independencies via d-separation, it
seems natural to want to construct graphs that include counterfactuals as
nodes, so that unconditional and conditional exchangeability can be directly
read off the graph.
A new type of graph—Single-world intervention graphs (SWIGs)— unify
the counterfactual and graphical approaches by explicitly including the coun-
terfactual variables on the graph. A SWIG depicts the variables and causalRichardson and Robins (2013)
showed that SWIGs overcome some
of the shortcomings of previously
proposed twin causal diagrams
(Balke and Pearl 1994).
relations that would be observed in a hypothetical world in which all individ-
uals received treatment level a. That is, a SWIG is a graph that represents
a counterfactual world created by a single intervention. In contrast, the vari-
ables on a standard causal diagram represent the actual world. A SWIG can
then be viewed as a function that transforms a given causal diagram under a
given intervention. The following examples describe this transformation.
Suppose the causal diagram in Figure 7.2 represents the observed study
96 Confounding
data. The SWIG in Figure 7.9 is a transformation of Figure 7.2 that represents
Figure 7.9
Figure 7.10
a world in which all individuals have received an intervention that sets their
treatment to the fixed value a.
In the SWIG, the treatment node is split into left and right sides which are
to be regarded as separate nodes (variables) once split. The right side encodes
the treatment value a under the intervention and inherits all the arrows that
were out of A in the original causal DAG. The left side encodes the value of
treatment A that would have been observed in the absence of intervention,
i.e., the natural value of treatment. It inherits all nodes that were into A on
the causal DAG because its causal inputs are the same in the intervened on
(counterfactual) world as in the actual world. Note that A does not have
an arrow into a because the value a is the same for all individuals, i.e., is a
constant in the intervened on world.
We assume that the natural value of treatment A is well defined even though
we are generally unable to measure it under intervention a. In some settings,
though, A may be measurable: recent experiments suggest that electroen-
cephalogram recordings can detect the choice individuals will make up to 1/2
second before individuals becomes conscious of their decision. If so, A could
actually be measured via electroencephalogram, while still leaving 1/2 second
to intervene and give treatment a.
In the SWIG, the outcome is Y
a
, the value of Y in the intervened on world.
Because the remaining variables are temporally prior to A, they are not affected
by the intervention and therefore take the same value as in the observed world.
i.e., they are not labeled as a counterfactual variable. In fact, any variable
that is a non-descendant of A need not be labeled as a counterfactual because,
under the faithfulness assumption (which we make), treatment has no causal
effect on its non-descendants for any individual. Under our causal model,Under an FFRCISTG model, it can
be shown that d-separation also
implies statistical independence on
the SWIG.
conditional exchangeability Y
a
⊥⊥A|L holds because all paths between Y
a
and
A are blocked after conditioning on L, i.e., Y
a
and A are d-separated given L.
Consider now the causal diagram in Figure 7.4 and the SWIG in Figure
7.10. Marginal exchangeability Y
a
⊥⊥A holds because, on the SWIG, all paths
between Y
a
and A are blocked (without conditioning on L). In contrast,
conditional exchangeability Y
a
⊥⊥A|L does not hold because, on the SWIG, theIn the single intervention world, a
is a constant and thus cannot af-
fect other variables. When draw-
ing SWIGs, however, we include ar-
rows from a as a convenient way to
keep track of the variables directly
affected by A in the original DAG.
path Y
a
←− U
1
−→ L ←− U
2
−→ A is open when the collider L is conditioned
on. This is why the marginal A-Y association is causal, but the conditional A-
Y association given L is not, and thus any method that adjusts for L results in
bias. These examples show how SWIGs unify the counterfactual and graphical
approaches. In fact it is straightforward to see that, on the SWIG, Y
a
is d-
separated from A given L if and only if L is a non-descendant of A that blocks
all backdoor paths from A to Y (see also Fine Point 7.4).
7.6 Confounding adjustment
Figure 7.11
In the absence of randomization, causal inference relies on the uncheckable
assumption that we have measured a set of variables L that is a sufficient
set for confounding adjustment, i.e., a set of non-descendants of treatment
A that includes enough variables to block all backdoor paths from A to Y .
Under this assumption of conditional exchangeability given L, standardization
and IP weighting can be used to compute the average causal effect in the
population. But, as discussed in Section 4.6, standardization and IP weighting
are not the only available methods to adjust for confounding in observational
7.6 Confounding adjustment 97
Fine Point 7.4
Confounders cannot be descendants of treatment, but can be in the future of treatment. Consider the causal
DAG in Figure 7.11. L is a descendant of treatment A that blocks all backdoor paths from A to Y . Unlike in Figures
7.4 and 7.7, conditioning on L does not cause selection bias because no collider path is opened. Rather, because the
causal effect of A on Y is solely through the intermediate variable L, conditioning on L completely blocks this pathway.
This example shows that adjusting for a variable L that blocks all backdoor paths does not eliminate bias when L is a
descendant of A.
Since conditional exchangeability Y
a
⊥⊥A|L implies that the adjustment for L eliminates all bias, it must be the case
that conditional exchangeability fails to hold and the average treatment effect E[Y
a=1
] −E[Y
a=0
] cannot be identified
in this example. This failure can be verified by analyzing the SWIG in Figure 7.12, which depicts a counterfactual world
in which A has been set to the value a. In this world, the factual variable L is replaced by the counterfactual variable
L
a
, i.e., the value of L that would have been observed if all individuals had received treatment value a. Since L
a
blocks
all paths from Y
a
to A we conclude that Y
a
⊥⊥A|L
a
holds, but we cannot conclude that conditional exchangeability
Y
a
⊥⊥A|L holds as L is not even on the graph. (Under an FFRCISTG, any independence that cannot be read off the
SWIG cannot be assumed to hold.) Therefore, we cannot ensure that the average treatment effect E[Y
a=1
] −E[Y
a=0
]
is identified from data on (L, A, Y ).
The problem arises because L is a descendant of A, not because L is in the future of A. If, in Figure 7.11, the arrow
from A to L did not exist, then L would be a non-descendant of A that blocks all the backdoor paths. Analogously,
on the SWIG in Figure 7.12, we can replace L
a
by L as A is no longer a cause of L (note Y
a
and A are now d-
separated by L). Therefore adjusting for L would eliminate all bias, even if L were still in the future of A. What
matters is the topology of the causal diagram (which variables cause which variables), not the time sequence of the
nodes. Rosenbaum (1984) and Robins (1986, section 11) give non-graphical discussions of the control of confounding
by temporally post-treatment variables.
studies. Methods that adjust for confounders L can be classified into two broad
categories:
Figure 7.12
• G-methods: Standardization, IP weighting, and g-estimation. These
methods (the ‘g’ stands for ‘generalized’) exploit conditional exchange-
ability given L to estimate the causal effect of A on Y in the entire
population or in any subset of the population. In our heart transplant
study, we used g-methods to adjust for confounding by disease severity
L in Sections 2.4 (standardization) and 2.5 (IP weighting). Part II de-
scribes model-based extensions of g-methods: the parametric g-formula
(standardization), IP weighting of marginal structural models, and g-
estimation of nested structural models.
• Conventional methods for stratification-based adjustment: Stratifica-
tion (including restriction) and matching. These methods exploit con-
ditional exchangeability given L to estimate the association between A
and Y in subsets defined by L. In our heart transplant study, we used
stratification-based methods to adjust for confounding by disease severity
L in Sections 4.4 (stratification) and 4.5 (matching). Part II describes theA common variation of stratifica-
tion and matching replaces each
individual’s variables L by the in-
dividual’s estimated probability of
receiving treatment Pr [A = 1|L]:
the propensity score (Rosenbaum
and Rubin 1983). See Chapter 15.
model-based extension of conventional stratification: outcome regression.
Standardization and IP weighting simulate the A-Y association in the pop-
ulation if backdoor paths involving the measured variables L did not exist. For
example, IP weighting achieves this by creating a pseudo-population in which
treatment A is independent of the measured confounders L, i.e., by “deleting”
the arrow from L to A. In contrast, conventional methods based on stratifica-
tion do not delete the arrow from L to A but rather compute the conditional
98 Confounding
effect in a subset of the observed population, which is represented by adding a
selection box. In Part III, focused on time-varying treatments, we describe why
“deleting” the arrow L → A is advantageous when using standardization or
IP weighting, and why g-estimation is the only generally valid stratification-
based method. The bias of conventional stratification-based methods is de-
scribed in Chapter 20. In settings with time-varying treatments, and therefore
time-varying confounders, g-methods are the methods of choice to adjust for
confounding because conventional stratification-based methods may result in
selection bias.
All the above methods require conditional exchangeability given L. How-
ever, confounding can sometimes be handled by methods that do not require
conditional exchangeability. Some examples of these methods are difference-
in-differences (Technical Point 7.3), instrumental variable estimation (Chapter
16), proximal inference (Technical Point 7.3), the front door criterion (Tech-
nical Point 7.4), and others. Unfortunately, these methods require alternative
assumptions that, like conditional exchangeability, are unverifiable. Therefore,
in practice, the validity of the resulting effect estimates is not guaranteed. The
choice of adjustment method will depend on which unverifiable assumptions—
either conditional exchangeability or the alternative conditions—are believed
more likely to hold in a particular setting.
Achieving conditional exchangeability may be an unrealistic goal in many
observational studies but, as discussed in Section 3.2, expert knowledge about
the causal structure can be used to get as close as possible to that goal. There-
fore, in observational studies, investigators measure many variables L (which
are non-descendants of treatment) in an attempt to ensure that the treated and
the untreated are conditionally exchangeable. The hope is that, even though
common causes may exist (confounding), the measured variables L are suf-
ficient to block all backdoor paths (no unmeasured confounding). However,
there is no guarantee that this attempt will be successful, which makes causal
inference from observational data a risky undertaking.
In addition, expert knowledge can be used to avoid adjusting for variables
that may introduce bias. At the very least, investigators should generallyA practical example of the ap-
plication of expert knowledge of
the causal structure to confounding
evaluation was described by Hern´an
et al (2002).
avoid adjustment for variables affected by either the treatment or the outcome.
Of course, thoughtful and knowledgeable investigators could believe that two
or more causal structures, possibly leading to different conclusions regarding
confounding and confounders, are equally plausible. In that case they would
perform multiple analyses and explicitly state the assumptions about causal
structure required for the validity of each. Unfortunately, one can never be
certain that the set of causal structures under consideration includes the true
one; this uncertainty is unavoidable with observational data.
Figure 7.13
There is a scientific consequence to the always present threat of confound-
ing in observational studies. Suppose you conducted an observational study
to quantify the effect of heart transplant A on death Y . You did your best
(e.g., consulting subject-matter experts) to identify and measure confounders
L, and assumed no unmeasured confounding after adjusting for L. A critic of
your study says “the inferences from this observational study may be incorrect
because of potential confounding.” The critic is not making a scientific state-
ment, but a logical one. Since the findings from any observational study may
be confounded, it is obviously true that those of your study can be confounded.
If the critic’s intent was to provide evidence about the shortcomings of your
particular study, he failed. His criticism is noninformative because he sim-
ply restated a characteristic of observational research that you and the critic
already knew before the study was conducted.
7.6 Confounding adjustment 99
To appropriately criticize your study, the critic needs to engage in a scien-
tific conversation. For example, the critic may cite experimental or observa-
tional evidence that contradict your findings, or he can say something along
Figure 7.14
Figure 7.15
the lines of “the inferences from this observational study may be incorrect
because of potential confounding due to cigarette smoking, a common cause
through which a backdoor path may remain open”. This latter option provides
you with a testable challenge to your assumption of no unmeasured confound-
ing. The burden of the proof is again yours. Your next move is to try and
adjust for smoking or, if data on smoking could not be obtained, to conduct a
sensitivity analysis to investigate the possible bias induced by smoking.
Though the above discussion was restricted to bias due to confounding, the
absence of biases due to selection and measurement is also needed for valid
causal inference from observational data. But, unlike confounding, these other
biases may arise in both randomized experiments and observational studies.
After having explored confounding in this chapter, the next chapter presents
another potential source of lack of exchangeability between the treated and the
untreated: selection of individuals into the analysis.
100 Confounding
Technical Point 7.3
Difference-in-differences and negative outcome controls. Suppose we want to compute the average causal effect
of aspirin A (1: yes; 0: no) on blood pressure Y , but there are unmeasured common causes U of A and Y such
as history of heart disease. Then we cannot compute the effect via standardization or IP weighting because there is
unmeasured confounding. But there is an alternative method that, under some conditions, may adjust for the unmeasured
confounding: the use of negative outcome controls (also known as “placebo tests”).
Suppose further that, for each individual in the population, we have also measured the value of the outcome right
before treatment was available. We refer to this pre-treatment outcome C as a negative outcome control (also referred
to as negative control outcome). As depicted in Figure 7.13, U is a cause of both Y and C, and treatment A is obviously
not a cause of the pre-treatment C. Now, even though the causal effect of A on C is known to be zero, the contrast
E [C|A = 1] − E [C|A = 0] is not zero because of confounding by U. In fact, E [C|A = 1] − E [C|A = 0] measures the
magnitude of confounding for the effect of A on C on the additive scale. If the magnitude of additive confounding for
the effect of A on the negative control outcome C is the same as for the effect of A on the true outcome Y , then
we can compute the effect of A on Y in the treated. Specifically, under the assumption of additive equi-confounding
E
Y
0
|A = 1
− E
Y
0
|A = 0
= E [C|A = 1] − E [C|A = 0], the effect is
E
Y
1
− Y
0
|A = 1
= (E [Y |A = 1] − E [Y |A = 0]) − (E [C|A = 1] − E [C|A = 0])
That is, the effect in the treated is equal to the association between treatment A and outcome Y (which is a mixture
of the causal effect and confounding) minus the confounding as measured by the association between A and C. Note
that the direct arrow from C to Y in Figure 7.13 is not necessary for C to be a negative outcome control.
This method for confounding adjustment is known as difference-in-differences (Card 1990, Meyer 1995, Angrist and
Krueger 1999). In practice, the method is often combined with adjustment for measured covariates using parametric
or semiparametric approaches (Abadie 2005). However, difference-in-differences is a somewhat restrictive approach to
negative outcome controls (Sofer et al. 2016): it requires measurement of the outcome both pre- and post-treatment
(or at least that the true outcome Y and the negative control outcome C are measured on the same scale) and it
requires additive equi-confounding. Sofer et al. (2016) describe more general methods that allow for Y and C to be on
different scales, rely on weaker versions of equi-confounding, and incorporate adjustment for measured covariates. For
a general introduction to the use of negative outcome controls to detect confounding, see Lipsitch et al. (2010) and
Flanders et al. (2011).
Surprisingly, when one has both a negative outcome control C and a negative treatment control Z, the causal effect
can be nonparametrically identified even in the presence of unmeasured confounders U under additional assumptions.
In fact, if U , C, and Z are discrete and C and Z have at least as many levels as does U, then the causal effect of A
on Y will quite generally be identified (Miao et al. 2018). This identification approach is referred to as proximal causal
inference (Cui et al. 2020). Figure 7.15 is one example in which C is a negative outcome control and Z is a negative
treatment control.
7.6 Confounding adjustment 101
Technical Point 7.4
The front door criterion. The causal diagram in Figure 7.14 depicts a setting in which the treatment A and the
binary outcome Y share an unmeasured cause U, and in which there is a variable M that fully mediates the effect of
A on Y and that shares no unmeasured causes with either A or Y . Under this causal structure, a data analyst cannot
directly use standardization (nor IP weighting) to compute the counterfactual risks Pr
Y
a=1
= 1
and Pr
Y
a=0
= 1
because the variable U, which is necessary to block the backdoor path between A and Y , is not available. Therefore,
the average causal effect of A on Y cannot be identified using the methods described in previous chapters. However,
Pearl (1995) showed that Pr [Y
a
= 1] is identified by the so-called front door formula
X
m
Pr [M = m|A = a]
X
a
′
Pr [Y = 1|M = m, A = a
′
] Pr [A = a
′
]
Pearl refers to this identification formula as front door adjustment because it relies on the existence of a path from A
and Y that, contrary to a backdoor path, goes through a descendant M of A that completely mediates the effect of A on
Y . Pearl often uses the term backdoor formula to refer to the identification formula that we refer to as standardization
or the point treatment g-formula (Robins 1986). A proof of the front door identification formula follows.
Note that Pr [Y
a
= 1] =
P
m
Pr [M
a
= m] Pr [Y
a
= 1|M
a
= m] and that, under Figure 7.14, Pr [M
a
= m] =
Pr [M = m|A = a] because there is no confounding for the effect of A on M (i.e., A⊥⊥M
a
), and Pr [Y
a
= 1|M
a
= m] =
P
a
′
Pr [Y = 1|M = m, A = a
′
] Pr [A = a
′
]. To prove the last equality, first note that Pr [Y
a
= 1|M
a
= m] =
Pr [Y
m
= 1] because (i) Y
a
= Y
m
when M
a
= m (A affects Y only through M in Figure 7.14) and (ii)
Y
m
⊥⊥M
a
by d-separation on a SWIG under the joint intervention in which M is set to m and A to a. Fi-
nally, by conditional exchangeability Y
m
⊥⊥M|A on the SWIG where we intervene on M alone, Pr [Y
m
= 1] =
P
a
′
Pr [Y = 1|M = m, A = a
′
] Pr [A = a
′
].
The above proof requires well-defined counterfactual outcomes Y
m
under interventions on M. In Technical Points
21.11 and 21.12 we present alternative proofs of the front door formula that do not require this condition.
102 Confounding
Chapter 8
SELECTION BIAS
Suppose an investigator conducted a randomized experiment to answer the causal question “does one’s looking
up to the sky make other pedestrians look up too?” She found a strong association between her looking up and
other pedestrians’ looking up. Does this association reflect a causal effect? Well, by definition of randomized
experiment, confounding bias is not expected in this study. However, there was another potential problem: The
analysis included only those pedestrians that, after having been part of the experiment, gave consent for their data
to be used. Shy pedestrians (those less likely to look up anyway) and pedestrians in front of whom the investigator
looked up (who felt tricked) were less likely to participate. Thus participating individuals in front of whom the
investigator looked up (a reason to decline participation) are less likely to be shy (an additional reason to decline
participation) and therefore more likely to look up. That is, the process of selection of individuals into the analysis
guarantees that one’s looking up is associated with other pedestrians’ looking up, regardless of whether one’s
looking up actually makes others look up.
An association created as a result of the process by which individuals are selected into the analysis is referred to
as selection bias. Unlike confounding, this type of bias is not due to the presence of common causes of treatment and
outcome, and can arise in both randomized experiments and observational studies. Like confounding, selection
bias is just a form of lack of exchangeability between the treated and the untreated. This chapter provides a
definition of selection bias and reviews the methods to adjust for it.
8.1 The structure of selection bias
The term “selection bias” encompasses various biases that arise from the proce-
dure by which individuals are selected into the analysis. Here we focus on bias
that would arise even if the treatment had a null effect on the outcome, i.e.,
selection bias under the null (as described in Section 6.5). The structure of se-
lection bias can be represented by using causal diagrams like the one in Figure
8.1, which depicts dichotomous treatment A, outcome Y , and their common
Figure 8.1 effect C. Suppose Figure 8.1 represents a study to estimate the effect of folic
acid supplements A given to pregnant women shortly after conception on the
fetus’s risk of developing a cardiac malformation Y (1: yes, 0: no) during the
first two months of pregnancy. The variable C represents death before birth.
A cardiac malformation increases mortality (arrow from Y to C), and folic
acid supplementation decreases mortality by reducing the risk of malforma-
tions other than cardiac ones (arrow from A to C). The study was restricted
to fetuses who survived until birth. That is, the study was conditioned on noPearl (1995) and Spirtes et al
(2000) used causal diagrams to de-
scribe the structure of bias resulting
from selection of individuals.
death C = 0 and hence the box around the node C.
The diagram in Figure 8.1 shows two sources of association between treat-
ment and outcome: 1) the open path A → Y that represents the causal effect
of A on Y , and 2) the open path A → C ← Y that links A and Y through
their (conditioned on) common effect C. An analysis conditioned on C will
generally result in an association between A and Y . We refer to this induced
association between the treatment A and the outcome Y as selection bias due
to conditioning on C. Because of selection bias, the associational risk ratio
104 Selection bias
Pr[Y = 1|A = 1, C = 0]/ Pr[Y = 1|A = 0, C = 0] does not equal the causal
risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
; association is not causation. If the
analysis were not conditioned on the common effect (collider) C, then the only
open path between treatment and outcome would be A → Y , and thus the
entire association between A and Y would be due to the causal effect of A on
Figure 8.2
Y . That is, the associational risk ratio Pr[Y = 1|A = 1]/ Pr[Y = 1|A = 0]
would equal the causal risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
; association
would be causation.
The causal diagram in Figure 8.2 shows another example of selection bias.
This diagram includes all variables in Figure 8.1 plus a node S representing
parental grief (1: yes, 0: no), which is affected by vital status at birth. Suppose
the study was restricted to non grieving parents S = 0 because the others were
unwilling to participate. As discussed in Chapter 6, conditioning on a variable
S affected by the collider C also opens the path A → C ← Y .
Figure 8.3
Figure 8.4
Figure 8.5
Figure 8.6
Both Figures 8.1 and 8.2 depict examples of selection bias in which the bias
arises because of conditioning on a common effect of treatment and outcome:
C in Figure 8.1 and S in Figure 8.2. This bias arises regardless of whether there
is an arrow from A to Y , i.e., it is selection bias under the null. Remember
that causal structures that result in bias under the null also cause bias when
the treatment has a non-null effect. Both confounding due to common causes
of treatment and outcome (see previous chapter) and selection bias due to
conditioning on common effects of treatment and outcome are examples of
bias under the null. However, selection bias under the null can be defined
more generally as illustrated by Figures 8.3 to 8.6.
Consider the causal diagram in Figure 8.3, which represents a follow-up
study of individuals with HIV infection to estimate the effect of certain an-
tiretroviral treatment A on the 3-year risk of death Y (to reduce clutter, there
is no arrow from A to Y ). The unmeasured variable U represents high level
of immunosuppression (1: yes, 0: no). Individuals with U = 1 have a greater
risk of death. Individuals who drop out from the study or are otherwise lost to
follow-up are censored (C = 1). Individuals with U = 1 are more likely to be
censored because the severity of their disease prevents them from participating
in the study. The effect of U on censoring C is mediated by the presence of
symptoms (fever, weight loss, diarrhea, and so on), CD4 count, and viral load
in plasma, all included in L, which could or could not be measured. (The
role of L, when measured, in data analysis is discussed in Section 8.5; in this
section, we take L to be unmeasured.) Individuals receiving treatment are at a
greater risk of experiencing side effects, which could lead them to dropout, as
represented by the arrow from A to C. The square around C indicates that the
analysis is restricted to individuals who remained uncensored (C = 0) because
those are the only ones in which Y can be assessed.
According to the rules of d-separation, conditioning on the collider C opens
the path A → C ← L ← U → Y and thus association flows from treatment A
to outcome Y , i.e., the associational risk ratio is not equal to 1 even though
the causal risk ratio is equal to 1. Figure 8.3 can be viewed as a simple
transformation of Figure 8.1: the association between Y and C resulting from
a direct effect of Y on C in Figure 8.1 is now the result of U , a common
cause of Y and C. Some intuition for this bias: If a treated individual with
treatment-induced side effects (and thereby at a greater risk of dropping out)
did in fact not drop out (C = 0), then it is generally less likely that a second
independent cause of dropping out (e.g., U = 1) was present. Therefore, an
inverse association between A and U would be expected in those who did
not drop out (C = 0). Because U is positively associated with the outcome
8.2 Examples of selection bias 105
Y , restricting the analysis to individuals who did not drop out of this study
induces an inverse association between A and Y .
The bias in Figure 8.3 is an example of selection bias that results from condi-
tioning on censoring C, which is a common effect of treatment A and of a cause
U of the outcome Y , rather than a common effect of treatment and outcome.
We now present three additional causal diagrams that could lead to selection
bias by differential loss to follow up. In Figure 8.4 prior treatment A has a
direct effect on symptoms L. Restricting the study to the uncensored individ-
uals again implies conditioning on the common effect C of A and U, thereby
introducing an association between treatment and outcome. Figures 8.5 and
8.6 are variations of Figures 8.3 and 8.4, respectively, in which there is a com-Figures 8.5 and 8.6 show examples
of M-bias mon cause W of A and another measured variable. W indicates unmeasured
lifestyle/personality/educational variables that determine both treatment (ar-
row from W to A) and either attitudes toward attending study visits (arrow
from W to C in Figure 8.5) or threshold for reporting symptoms (arrow from
W to L in Figure 8.6).More generally, selection bias can
be defined as the bias resulting from
conditioning on the common ef-
fect of two variables, one of which
is either the treatment or associ-
ated with the treatment, and the
other is either the outcome or asso-
ciated with the outcome (Hern´an,
Hern´andez-D´ıaz, and Robins 2004).
We have described some different causal structures, depicted in Figures
8.1-8.6, that may lead to selection bias under the null. In all these cases, the
bias is the result of selection on a common effect of two other variables in the
diagram, i.e., a collider. We will use the term selection bias to refer to all
biases that arise from conditioning on a common effect of two variables, one of
which is either the treatment or a cause of treatment, and the other is either
the outcome or a cause of the outcome. We now describe some examples of
selection bias that share this structure.
8.2 Examples of selection bias
Consider the following examples of bias due to the mechanism by which indi-
viduals are selected into the analysis:
• Differential loss to follow-up: This is precisely the bias described in the
previous section and summarized in Figures 8.3-8.6. It is also referred to
as bias due to informative censoring.The distinction between the two
structures leading to lack of ex-
changeability is not universally
made across disciplines. Condi-
tional exchangeability is often re-
ferred as “weak ignorability” or “ig-
norable treatment assignment” in
statistics (Rosenbaum and Rubin
1983, Rosenbaum 2002), “selection
on observables” in the social sci-
ences (Barnow, Cain, and Gold-
berger, 1980), and “no ommitted
variable bias” or “exogeneity” in
econometrics (Imbens, 2004).
• Missing data bias,nonresponse bias: The variable C in Figures 8.3-8.6
can represent missing data on the outcome for any reason, not just as a
result of loss to follow up. For example, individuals could have missing
data because they are reluctant to provide information or because they
miss study visits. Regardless of the reasons why data on Y are missing,
restricting the analysis to individuals with complete data (C = 0) may
result in bias.
• Healthy worker bias: Figures 8.3–8.6 can also describe a bias that could
arise when estimating the effect of an occupational exposure A (e.g., a
chemical) on mortality Y in a cohort of factory workers. The underlying
unmeasured true health status U is a determinant of both death Y and
of being at work C (1: no, 0: yes). The study is restricted to individuals
who are at work (C = 0) at the time of outcome ascertainment. (L
could be the result of blood tests and a physical examination.) Being
exposed to the chemical reduces the probability of being at work in the
near future, either directly (e.g., exposure can cause disabling asthma),
like in Figures 8.3 and 8.4, or through a common cause W (e.g., certain
106 Selection bias
Fine Point 8.1
Selection bias in case-control studies. Figure 8.1 can be used to represent selection bias in a case-control study.
Suppose a certain investigator wants to estimate the effect of postmenopausal estrogen treatment A on coronary heart
disease Y . The variable C indicates whether a woman in the study population (the underlying cohort, in epidemiologic
terms) is selected for the case-control study (1: no, 0: yes). The arrow from disease status Y to selection C indicates
that cases in the population are more likely to be selected than noncases, which is the defining feature of a case-control
study. In this particular case-control study, the investigator decided to select controls (Y = 0) preferentially among
women with a hip fracture. Because treatment A has a protective causal effect on hip fracture, the selection of controls
with hip fracture implies that treatment A now has a causal effect on selection C. This effect of A on C is represented
by the arrow A → C. One could add an intermediate node F (representing hip fracture) between A and C, but that is
unnecessary for our purposes.
In a case-control study, the association measure (the treatment-outcome odds ratio) is by definition conditional on
having been selected into the study (C = 0). If individuals with hip fracture are oversampled as controls, then the
probability of control selection depends on a consequence of treatment A (as represented by the path from A to C)
and “inappropriate control selection” bias will occur. Again, this bias arises because we are conditioning on a common
effect C of treatment and outcome. A heuristic explanation of this bias follows. Among individuals selected for the
study (C = 0), controls are more likely than cases to have had a hip fracture. Therefore, because estrogens lower
the incidence of hip fractures, a control is less likely to be on estrogens than a case, and hence the A-Y odds ratio
conditional on C = 0 would be greater than the causal odds ratio in the population. Other forms of selection bias
in case-control studies, including some biases described by Berkson (1946) and incidence-prevalence bias, can also be
represented by Figure 8.1 or modifications of it, as discussed by Hern´an, Hern´andez-D´ıaz, and Robins (2004).
exposed jobs are eliminated for economic reasons and the workers laid
off) like in Figures 8.5 and 8.6.
• Self-selection bias, volunteer bias: Figures 8.3-8.6 can also represent a
study in which C is agreement to participate (1: no, 0: yes), A is cigaretteBerkson (1955) described the struc-
ture of bias due to self-selection. smoking, Y is coronary heart disease, U is family history of heart disease,
and W is healthy lifestyle. (L is any mediator between U and C such as
heart disease awareness.) Under any of these structures, selection bias
may be present if the study is restricted to those who volunteered or
elected to participate (C = 0).
• Selection affected by treatment received before study entry: Suppose that
C in Figures 8.3-8.6 represents selection into the study (1: no, 0: yes)
and that treatment A took place before the study started. If treatmentRobins, Hern´an, and Rotnitzky
(2007) used causal diagrams to de-
scribe the structure of bias due to
the effect of pre-study treatments
on selection into the study.
affects the probability of being selected into the study, then selection
bias is expected. The case of selection bias arising from the effect of
treatment on selection into the study can be viewed as a generalization
of self-selection bias. This bias may be present in any study that at-
tempts to estimate the causal effect of a treatment that occurred before
the study started or in which treatment includes a pre-study component.
For example, selection bias may arise when treatment is measured as the
lifetime exposure to certain factor (medical treatment, lifestyle behav-
ior...) in a study that recruited 50 year-old participants. In addition to
selection bias, it is also possible that there exists unmeasured confound-
ing for the pre-study component of treatment if confounders were only
measured during the study.
In addition to the biases described here, as well as in Fine Point 8.1 and
Technical Point 8.1, causal diagrams have been used to characterize various
8.3 Selection bias and confounding 107
other biases that arise from conditioning on a common effect. These examples
show that selection bias may occur in retrospective studies—those in which data
on treatment A are collected after the outcome Y occurs—and in prospective
studies—those in which data on treatment A are collected before the outcome
Y occurs. Further, these examples show that selection bias may occur both inFor example, selection bias may be
induced by attempts to eliminate
bias from ascertainment (Robins
2001), to estimate direct effects
(Cole and Hern´an 2002), and by
conventional adjustment for vari-
ables affected by previous treat-
ment (see Part III).
observational studies and in randomized experiments.
Take Figures 8.3 and 8.4, which could depict either an observational study
or an experiment in which treatment A is randomly assigned, because there are
no common causes of A and any other variable. Individuals in both randomized
experiments and observational studies may be lost to follow-up or drop out of
the study before their outcome is ascertained. When this happens, the risk
Pr[Y = 1|A = a] cannot be computed because the value of the outcome Y is
unknown for the censored individuals (C = 1). Therefore only the risk among
the uncensored Pr[Y = 1|A = a, C = 0] can be computed. This restriction of
the analysis to the uncensored individuals may induce selection bias because
uncensored individuals who remained through the end of the study (C = 0)
may not be exchangeable with individuals that were lost (C = 1).
Hence a key difference between confounding and selection bias: random-
ization protects against confounding, but not against selection bias when the
selection occurs after the randomization. On the other hand, no bias arises
in randomized experiments from selection into the study before treatment is
assigned. For example, only volunteers who agree to participate are enrolled
in randomized clinical trials, but such trials are not affected by volunteer bias
because participants are randomly assigned to treatment only after agreeing to
participate (C = 0). Thus none of Figures 8.3-8.6 can represent volunteer bias
in a randomized trial. Figures 8.3 and 8.4 are eliminated because treatment
cannot cause agreement to participate C. Figures 8.5 and 8.6 are eliminated
because, as a result of the random treatment assignment, there cannot exist a
common cause of treatment and any other variable.
8.3 Selection bias and confounding
Figure 8.7
In this and the previous chapter, we describe two reasons why the treated and
the untreated may not be exchangeable: 1) the presence of common causes of
treatment and outcome, and 2) conditioning on common effects of treatment
and outcome (or causes of them). We refer to biases due to the presence of
common causes as “confounding” and to those due to conditioning on common
effects as “selection bias.” This structural definition provides a clear-cut clas-
sification of confounding and selection bias, even though it might not coincide
perfectly with the traditional terminology of some disciplines. For example,
statisticians and econometricians often use the term “selection bias” to refer
to both types of biases. Their rationale is that in both cases the bias is due
to selection: selection of individuals into the analysis (the structural “selection
bias”) or selection of individuals into a treatment (the structural “confound-
ing”). Our goal, however, is not to be normative about terminology, but ratherFor the same reason, social scien-
tists often refer to unmeasured con-
founding as selection on unobserv-
ables.
to emphasize that, regardless of the particular terms chosen, there are two dis-
tinct causal structures that lead to bias.
The end result of both structures is lack of exchangeability between the
treated and the untreated—which implies that these two biases occur even
under the null. For example, consider a study restricted to firefighters that
aims to estimate the causal effect of being physically active A on the risk
108 Selection bias
Technical Point 8.1
The built-in selection bias of hazard ratios. The causal DAG in Figure 8.8 describes a randomized experiment of the
effect of heart transplant A on death at times 1 (Y
1
) and 2 (Y
2
). The arrow from A to Y
1
represents that transplant
decreases the risk of death at time 1. The lack of an arrow from A to Y
2
indicates that A has no direct effect on death
at time 2. That is, heart transplant does not influence the survival status at time 2 of any individual who would survive
past time 1 when untreated (and thus when treated). U is an unmeasured haplotype that decreases the individual’s risk
of death at all times. Because of the absence of confounding, the associational risk ratios aRR
AY
1
=
Pr[Y
1
=1|A=1]
Pr[Y
1
=1|A=0]
and
aRR
AY
2
=
Pr[Y
2
=1|A=1]
Pr[Y
2
=1|A=0]
are unbiased measures of the effect of A on death at times 1 and 2, respectively. Even though
A has no direct effect on Y
2
, aRR
AY
2
will be less than 1 because it is a measure of the effect of A on total mortality
through time 2.
Consider now the time-specific hazard ratio (which, for all practical purposes, is equivalent to the rate ratio). In
discrete time, the hazard of death at time 1 is the probability of dying at time 1 and thus the associational hazard ratio
is the same as aRR
AY
1
. However, the hazard at time 2 is the probability of dying at time 2 among those who survived
past time 1. Thus, the associational hazard ratio at time 2 is then aRR
AY
2
|Y
1
=0
=
Pr[Y
2
=1|A=1,Y
1
=0]
Pr[Y
2
=1|A=0,Y
1
=0]
. The square
around Y
1
in Figure 8.8 indicates this conditioning. Treated survivors of time 1 are less likely than untreated survivors of
time 1 to have the protective haplotype U (because treatment can explain their survival) and therefore are more likely
to die at time 2. That is, conditional on Y
1
, treatment A is associated with a higher mortality at time 2. Thus, the
hazard ratio at time 1 is less than 1, whereas the hazard ratio at time 2 is greater than 1, i.e., the hazards have crossed.
We conclude that the hazard ratio at time 2 is a biased estimate of the direct effect of treatment on mortality at time
2. The bias is selection bias arising from conditioning on a common effect Y
1
of treatment A and of U , which is a cause
of Y
2
that opens the associational path A → Y
1
← U → Y
2
between A and Y
2
. In the survival analysis literature, an
unmeasured cause of death that is marginally unassociated with treatment such as U is often referred to as a frailty .
In contrast, the conditional hazard ratio aRR
AY
2
|Y
1
=0,U
is 1 within each stratum of U because the path A → Y
1
←
U → Y
2
is now blocked by conditioning on the non-collider U. Thus, the conditional hazard ratio correctly indicates
the absence of a direct effect of A on Y
2
. That the unconditional hazard ratio aRR
AY
2
|Y
1
=0
differs from the stratum-
specific hazard ratios aRR
AY
2
|Y
1
=0,U
, even though U is independent of A, shows the noncollapsibility of the hazard
ratio (Greenland, 1996b). Unfortunately, the unbiased measure aRR
AY
2
|Y
1
=0,U
of the direct effect of A on Y
2
cannot
be computed because U is unobserved. In the absence of data on U , it is impossible to know whether A has a direct
effect on Y
2
. That is, the data cannot determine whether the true causal DAG generating the data was that in Figure
8.8 or in Figure 8.9. All of the above applies to both observational studies and randomized experiments.
of heart disease Y as represented in Figure 8.7. For simplicity, we assume
Figure 8.8
Figure 8.9
that, unknown to the investigators, A does not cause Y . Parental socioe-
conomic status L affects the risk of becoming a firefighter C and, through
childhood diet, of heart disease Y . Attraction toward activities that involve
physical activity (an unmeasured variable U ) affects the risk of becoming a
firefighter and of being physically active (A). U does not affect Y , and L does
not affect A. According to our terminology, there is no confounding because
there are no common causes of A and Y . Thus, the associational risk ratio
Pr [Y = 1|A = 1] / Pr [Y = 1|A = 0] is expected to equal the causal risk ratio
Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
= 1.
However, in a study restricted to firefighters (C = 0), the associational
and causal risk ratios would differ because conditioning on a common effect C
of causes of treatment and outcome induces selection bias resulting in lack of
exchangeability of the treated and untreated firefighters. To the study investi-
gators, the distinction between confounding and selection bias is moot because,
regardless of nomenclature, they must adjust for L to make the treated and
the untreated firefighters comparable. This example demonstrates that a struc-
tural classification of bias does not always have consequences for the analysis
8.4 Selection bias and censoring 109
of a study. Indeed, for this reason, many epidemiologists use the term “con-
founder” for any variable L that needs to be adjusted for, regardless of whether
the lack of exchangeability is the result of conditioning on a common effect or
the result of a common cause of treatment and outcome.
There are, however, advantages of adopting a structural approach to the
classification of sources of non-exchangeability. First, the structure of the
problem frequently guides the choice of analytical methods to reduce or avoid
the bias. For example, in longitudinal studies with time-varying treatments,
identifying the structure allows us to detect situations in which adjustment
for confounding via stratification would introduce selection bias (see Part III).
In those cases, g-methods are a better alternative. Second, even when under-
standing the structure of bias does not have implications for data analysis (like
in the firefighters’ study), it could still help study design. For example, inves-
tigators running a study restricted to firefighters should make sure that they
collect information on joint risk factors for the outcome Y and for the selection
variable C (i.e., becoming a firefighter), as described in the first example ofThe choice of terminology usually
has no practical consequences, but
disregard for the causal structure
may lead to apparent paradoxes.
For example, the so-called Simp-
son’s paradox (1951) was the re-
sult of ignoring the difference be-
tween common causes and common
effects. Interestingly, Blyth (1972)
failed to grasp the causal structure
of the paradox in Simpson’s exam-
ple and misrepresented it as an ex-
treme case of confounding. Be-
cause most people read Blyth’s pa-
per but not Simpson’s paper, the
misunderstanding was perpetuated.
See Hern´an, Clayton, and Keiding
(2011) for details.
confounding in Section 7.1. Third, selection bias resulting from conditioning
on pre-treatment variables (e.g., being a firefighter) could explain why cer-
tain variables behave as “confounders” in some studies but not others. In our
example, parental socioeconomic status L would not necessarily need to be
adjusted for in studies not restricted to firefighters. Finally, causal diagrams
enhance communication among investigators and may decrease the occurrence
of misunderstandings.
As an example of the last point, consider the “healthy worker bias”, which
in the previous section we described as a bias that arises from conditioning on
the variable C—a common effect of (a cause of) treatment and (a cause of) the
outcome. Thus the bias can be represented by the causal diagrams in Figures
8.3-8.6. However, the term “healthy worker bias” is also used to describe the
bias that occurs when comparing the risk in certain group of workers with that
in a group of individuals from the general population.
This second bias can be depicted by the causal diagram in Figure 7.1 in
which L represents health status, A represents membership in the group of
workers, and Y represents the outcome of interest. There are arrows from L to
A and Y because being healthy affects job type and risk of subsequent outcome,
respectively. In this case, the bias is caused by the common cause L and we
would refer to it as confounding. The use of causal diagrams to represent the
structure of the “healthy worker bias” prevents any confusions that may arise
from employing the same term for different sources of non-exchangeability.
All the above considerations ignore the magnitude or direction of selec-
tion bias and confounding. However, it is possible that some noncausal paths
opened by conditioning on a collider are weak and thus induce little bias. Be-
cause selection bias is not an “all or nothing” issue, in practice, it is important
to consider the expected direction and magnitude of the bias (see Fine Point
8.2).
8.4 Selection bias and censoring
Suppose an investigator conducted a marginally randomized experiment to
estimate the average causal effect of wasabi intake on the one-year risk of
death (Y = 1). Half of the 60 study participants were randomly assigned to
eating meals supplemented with wasabi (A = 1) until the end of follow-up or
110 Selection bias
death, whichever occurred first. The other half were assigned to meals that
contained no wasabi (A = 0). After 1 year, 17 individuals died in each group.
That is, the associational risk ratio Pr [Y = 1|A = 1] / Pr [Y = 1|A = 0] was 1.
Because of randomization, the causal risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
is also expected to be 1. (If ignoring random variability bothers you, please
imagine the study had 60 million patients rather than 60.)
Unfortunately, the investigator could not observe the 17 deaths that oc-
curred in each group because many patients were lost to follow-up, or censored,
before the end of the study (i.e., death or one year after treatment assignment).
The proportion of censoring (C = 1) was higher among patients with heart dis-
ease (L = 1) at the start of the study and among those assigned to wasabi sup-
plementation (A = 1). In fact, only 9 individuals in the wasabi group and 22
individuals in the other group were not lost to follow-up. The investigator ob-
served 4 deaths in the wasabi group and 11 deaths in the other group. That is,
the associational risk ratio Pr [Y = 1|A = 1, C = 0] / Pr [Y = 1|A = 0, C = 0]
was (4/9)/(11/22) = 0.89 among the uncensored. The risk ratio of 0.89 in
the uncensored differs from the causal risk ratio of 1 in the entire population:
There is selection bias due to conditioning on the common effect C.
The causal diagram in Figure 8.3 depicts the relation between the variables
L, A, C, and Y in the randomized trial of wasabi. U represents atherosclerosis,
an unmeasured variable, that affects both heart disease L and death Y . Figure
8.3 shows that there are no common causes of A and Y , as expected in a
marginally randomized experiment, and thus there is no need to adjust for
confounding to compute the causal effect of A on Y . On the other hand,
Figure 8.3 shows that there is a common cause U of C and Y . The presence
of this backdoor path C ← L ← U → Y implies that, were the investigator
interested in estimating the causal effect of censoring C on Y (which is null in
Figure 8.3), she would have to adjust for confounding due to the common cause
U. The backdoor criterion says that such adjustment is possible because the
measured variable L can be used to block the backdoor path C ← L ← U → Y .
The causal contrast we have considered so far is “the risk if everybody
had been treated”, Pr
Y
a=1
= 1
, versus “the risk if everybody had remained
untreated”, Pr
Y
a=0
= 1
, and this causal contrast does not involve C at all.
Why then are we talking about confounding for the causal effect of C? It turns
out that the causal contrast of interest needs to be modified in the presence
of censoring or, in general, of selection. Because selection bias would not exist
if everybody had been uncensored C = 0, we would like to consider a causal
contrast that reflects what would have happened in the absence of censoring.
Let Y
a=1,c=0
be an individual’s counterfactual outcome if he had received
treatment A = 1 and he had remained uncensored C = 0. Similarly, let
Y
a=0,c=0
be an individual’s counterfactual outcome if he had not received
treatment A = 0 and he had remained uncensored C = 0. Our causal contrast
of interest is now “the risk if everybody had been treated and had remained
uncensored”, Pr
Y
a=1,c=0
= 1
, versus “the risk if everybody had remained
untreated and uncensored”, Pr
Y
a=0,c=0
= 1
.For example, we may want to com-
pute the causal risk ratio
E
Y
a=1,c=0
/ E
Y
a=0,c=0
or the causal risk difference
E
Y
a=1,c=0
− E
Y
a=0,c=0
.
Often it is reasonable to assume that censoring does not have a causal
effect on the outcome (an exception would be a setting in which being lost to
follow-up prevents people from getting additional treatment). Because of the
lack of effect of censoring C on the outcome Y , one might imagine that the
definition of causal effect could ignore censoring, i.e., that we could omit the
superscript c = 0. However, omitting the superscript would obscure the fact
that considerations about confounding for C become central when computing
the causal effect of A on Y in the presence of selection bias. In fact, when
8.5 How to adjust for selection bias 111
conceptualizing the causal contrast of interest in terms of Y
a,c=0
, we can think
of censoring C as just another treatment. That is, the goal of the analysis isIn causal diagrams with no arrow
from censoring C to the observed
outcome Y , we could replace Y by
the counterfactual outcome Y
c=0
and add arrows Y
c=0
−→ Y and
C −→ Y .
to compute the causal effect of a joint intervention on A and C. To eliminate
selection bias for the effect of treatment A, we need to adjust for confounding
for the effect of treatment C.
Since censoring C is now viewed as a treatment, it follows that we will need
to (i) ensure that the identifiability conditions of exchangeability, positivity,
and consistency hold for C as well as for A, and (ii) use analytical methods
that are identical to those we would have to use if we wanted to estimate the
effect of censoring C. Under these identifiability conditions and using these
methods, selection bias can be eliminated via analytic adjustment and, in the
absence of measurement error and confounding, the causal effect of treatment
A on outcome Y can be identified. The next section explains how to do so.
8.5 How to adjust for selection bias
Though selection bias can sometimes be avoided by an adequate design (see
Fine Point 8.1), it is often unavoidable. For example, loss to follow up, self-
selection, and, in general, missing data leading to bias can occur no matter how
careful the investigator. In those cases, the selection bias needs to be explicitly
corrected in the analysis. This correction can sometimes be accomplished by
IP weighting (or by standardization), which is based on assigning a weight W
C
to each selected individual (C = 0) so that she accounts in the analysis not
only for herself, but also for those like her, i.e., with the same values of L and
A, who were not selected (C = 1). The IP weight W
C
is the inverse of the
probability of her selection Pr [C = 0|L, A].
To describe the application of IP weighting for selection bias adjustment
consider again the wasabi randomized trial described in the previous section.
The tree graph in Figure 8.10 presents the trial data. Of the 60 individuals inWe have described IP weights to
adjust for confounding, W
A
=
1/f (A|L), and selection bias.
W
C
= 1/ Pr[C = 0|A, L]. When
both confounding and selection bias
exist, the product weight W
A
W
C
can be used to adjust simultane-
ously for both biases under assump-
tions described in Chapter 12 and
Part III.
the trial, 40 had (L = 1) and 20 did not have (L = 0) heart disease at the time
of randomization. Regardless of their L status, all individuals had a 50/50
chance of being assigned to wasabi supplementation (A = 1). Thus 10 individ-
uals in the L = 0 group and 20 in the L = 1 group received treatment A = 1.
This lack of effect of L on A is represented by the lack of an arrow from L to A
in the causal diagram of Figure 8.3. The probability of remaining uncensored
varies across branches in the tree. For example, 50% of the individuals without
heart disease that were assigned to wasabi (L = 0, A = 1), whereas 60% of
the individuals with heart disease that were assigned to no wasabi (L = 1,
A = 0), remained uncensored. This effect of A and L on C is represented
by arrows from A and L into C in the causal diagram of Figure 8.3. Finally,
the tree shows how many people would have died (Y = 1) both among the
uncensored and the censored individuals. Of course, in real life, investigators
would never know how many deaths occurred among the censored individuals.
It is precisely the lack of this knowledge which forces investigators to restrict
the analysis to the uncensored, opening the door for selection bias. Here we
show the deaths in the censored to document that, as depicted in Figure 8.3,
treatment A is marginally independent of Y , and censoring C is independent
of Y within levels of L. It can also be checked that the risk ratio in the entire
population (inaccessible to the investigator) is 1 whereas the risk ratio in the
uncensored (accessible to the investigator) is 0.89.
112 Selection bias
Figure 8.10
Let us now describe the intuition behind the use of IP weighting to adjust
for selection bias. Look at the bottom of the tree in Figure 8.10. There
are 20 individuals with heart disease (L = 1) who were assigned to wasabi
supplementation (A = 1). Of these, 4 remained uncensored and 16 were lost
to follow-up. That is, the conditional probability of remaining uncensored in
this group is 1/5, i.e., Pr[C = 0|L = 1, A = 1] = 4/20 = 0.2. In an IP weighted
analysis the 16 censored individuals receive a zero weight (i.e., they do not
contribute to the analysis), whereas the 4 uncensored individuals receive a
weight of 5, which is the inverse of their probability of being uncensored (1/5).
IP weighting replaces the 20 original individuals by 5 copies of each of the
4 uncensored individuals. The same procedure can be repeated for the other
branches of the tree, as shown in Figure 8.11, to construct a pseudo-population
of the same size as the original study population but in which nobody is lost to
follow-up. (We let the reader derive the IP weights for each branch of the tree.)
The associational risk ratio in the pseudo-population is 1, the same as the risk
ratio Pr
Y
a=1,c=0
= 1
/ Pr
Y
a=0,c=0
= 1
that would have been computed in
the original population if nobody had been censored.
8.5 How to adjust for selection bias 113
Figure 8.11
The association measure in the pseudo-population equals the effect measure
in the original population if the following three identifiability conditions are
met.
First, the average outcome in the uncensored individuals must equal the
unobserved average outcome in the censored individuals with the same val-
ues of A and L. This provision will be satisfied if the probability of selection
Pr[C = 0|L = 1, A = 1] is calculated conditional on treatment A and on all
additional factors that independently predict both selection and the outcome,
that is, if the variables in A and L are sufficient to block all backdoor paths
between C and Y . Unfortunately, one can never be sure that these additional
factors were identified and recorded in L, and thus the causal interpretation
of the resulting adjustment for selection bias depends on this untestable ex-
changeability assumption.
Second, IP weighting requires that all conditional probabilities of being
uncensored given A and the variables in L must be greater than zero. Note
this positivity condition is required for the probability of being uncensored
(C = 0) but not for the probability of being censored (C = 1) because we are
114 Selection bias
not interested in inferring what would have happened if study individuals had
been censored, and thus there is no point in constructing a pseudo-population
in which everybody is censored. For example, the tree in Figure 8.10 shows
that Pr[C = 1|L = 0, A = 0] = 0, but this zero does not affect our ability to
construct a pseudo-population in which nobody is censored.
The third condition is consistency, including sufficiently well-defined inter-
ventions. IP weighting is used to create a pseudo-population in which censoring
C has been abolished, and in which the effect of the treatment A is the same
as in the original population. Thus, the pseudo-population effect measure is
equal to the effect measure had nobody been censored. This effect measure
may be relatively well defined when censoring is the result of loss to follow up
or nonresponse, but not when censoring is defined as the occurrence of a com-
peting event. For example, in a study aimed at estimating the effect of certainA competing event is an event that
prevents the outcome of interest
from happening. A typical exam-
ple of competing event is death be-
cause, once an individual dies, no
other outcomes can occur.
treatment on the risk of Alzheimer’s disease, death from other causes (cancer,
heart disease, and so on) is a competing event. Defining death as a form of
censoring is problematic: we might not wish to base our effect estimates on a
pseudo-population in which all other causes of death have been removed, be-
cause it is unclear even conceptually what sort of intervention would produce
such a population. Also, no feasible intervention could possibly remove just
one cause of death without affecting the others as well.
Finally, one could argue that IP weighting is not necessary to adjust for
selection bias in a setting like that described in Figure 8.3. Rather, one might
attempt to remove selection bias by stratification (i.e., by estimating the ef-
fect measure conditional on the L variables) rather than by IP weighting.
Stratification could yield unbiased conditional effect measures within levels of
Figure 8.12
Figure 8.13
L because conditioning on L is sufficient to block the backdoor path from C
to Y . That is, the conditional risk ratio
Pr [Y = 1|A = 1, C = 0, L = l] / Pr [Y = 1|A = 0, C = 0, L = l]
can be interpreted as the effect of treatment among the uncensored with L = l.
For the same reason, under the null, stratification would work (i.e., it would
provide an unbiased conditional effect measure) if the data can be represented
by the causal structure in Figure 8.5. Stratification, however, would not work
under the structure depicted in Figures 8.4 and 8.6.
Take Figure 8.4. Conditioning on L blocks the backdoor path from C to Y
but also opens the path A → L ← U → Y from A to Y because L is a collider
on that path. Thus, even if the causal effect of A on Y is null, the conditional
(on L) risk ratio would be generally different from 1. And similarly for Figure
8.6. In contrast, IP weighting appropriately adjusts for selection bias under
Figures 8.3-8.6 because this approach is not based on estimating effect measures
conditional on the covariates L, but rather on estimating unconditional effect
measures after reweighting the individuals according to their treatment and
their values of L.
This is the first time we discuss a situation in which stratification cannot
be used to validly compute the causal effect of treatment, even if the three
conditions of exchangeability, positivity, and consistency hold. We will discuss
other situations with a similar structure in Part III when considering the effect
of time-varying treatments.
8.6 Selection without bias 115
8.6 Selection without bias
The causal diagram in Figure 8.12 represents a hypothetical study with di-
chotomous variables surgery A, certain genetic haplotype E, and death Y .
According to the rules of d-separation, surgery A and haplotype E are (i)
Figure 8.14
Figure 8.15
Figure 8.16
marginally independent, i.e., the probability of receiving surgery is the same
for people with and without the genetic haplotype, and (ii) associated con-
ditionally on Y , i.e., the probability of receiving surgery varies by haplotype
when the study is restricted to, say, the survivors (Y = 0).
Indeed conditioning on the common effect Y of two independent causes A
and E always induces a conditional association between A and E in at least
one of the strata of Y (say, Y = 1). However, there is a special situation under
which A and E remain conditionally independent within the other stratum
(say, Y = 0).
Suppose A and E affect survival through totally independent mechanisms
in such a way that E cannot possibly modify the effect of A on Y , and vice
versa. For example, suppose that the surgery A affects survival through the
removal of a tumor, whereas the haplotype E affects survival through increasing
levels of low-density lipoprotein-cholesterol levels resulting in an increased risk
of heart attack (whether or not a tumor is present). In this scenario, we can
consider 3 cause-specific mortality variables: death from tumor Y
A
, death from
heart attack Y
E
, and death from any other causes Y
O
. The observed mortality
variable Y is equal to 1 (death) when Y
A
or Y
E
or Y
O
is equal to 1, and Y is
equal to 0 (survival) when Y
A
and Y
E
and Y
O
equal 0. The causal diagram in
Figure 8.13, an expansion of that in Figure 8.12, represents a causal structure
linking all these variables. We assume data on underlying cause of death (Y
A
,
Y
E
, Y
O
) are not recorded and thus the only measured variables are those in
Figure 8.12 (A, E, Y ).
Because the arrows from Y
A
, Y
E
and Y
O
to Y are deterministic, condition-
ing on observed survival (Y = 0) is equivalent to simultaneously conditioning
on Y
A
= 0, Y
E
= 0, and Y
O
= 0 as well, i.e., conditioning on Y = 0 implies
Y
A
= Y
E
= Y
O
= 0. As a consequence, we find by applying d-separation to
Figure 8.13 that A and E are conditionally independent given Y = 0, i.e.,
when conditioning on collider Y = 0, the path between A and E through
Y is blocked by conditioning on the non-colliders Y
A
, Y
E
and Y
O
. On the
other hand, conditioning on death Y = 1 does not imply conditioning on any
specific values of Y
A
, Y
E
and Y
O
as the event Y = 1 is compatible with 7 pos-
sible unmeasured events: (Y
A
= 1, Y
E
= 0, Y
O
= 0), (Y
A
= 0, Y
E
= 1, Y
O
= 0),
(Y
A
= 0, Y
E
= 0, Y
O
= 1), (Y
A
= 1, Y
E
= 1, Y
O
= 0), (Y
A
= 0, Y
E
= 1, Y
O
= 1),
(Y
A
= 1, Y
E
= 0, Y
O
= 1), and (Y
A
= 1, Y
E
= 1, Y
O
= 1). Thus, A and E are
associated given Y = 1, i.e., when conditioning on collider Y = 1, the path
between A and E through Y is not blocked.
In contrast with the situation represented in Figure 8.13, the variables
A and E will not be independent conditionally on Y = 0 when one of the
situations represented in Figures 8.14-8.16 occur. If A and E affect survival
through a common mechanism, then there will exist an arrow either from A
to Y
E
or from E to Y
A
, as shown in Figure 8.14. In that case, A and E
will be dependent within both strata of Y . Similarly, if Y
A
and Y
E
are not
independent because of a common cause V as shown in Figure 8.15, A and E
will be dependent within both strata of Y . Finally, if the causes Y
A
and Y
O
,
and Y
E
and Y
O
, are not independent because of common causes W
1
and W
2
as
shown in Figure 8.16, then A and E will also be dependent within both strata
of Y . When the data can be summarized by Figure 8.13, we say that the data
116 Selection bias
Technical Point 8.2
Multiplicative survival model. When the conditional probability of survival Pr [Y = 0|E = e, A = a] given A and E is
equal to a product g(e)h(a) of functions of e and a, we say that a multiplicative survival model holds. A multiplicative
survival model
Pr [Y = 0|E = e, A = a] = g(e)h(a)
is equivalent to a model that assumes the survival ratio Pr [Y = 0|E = e, A = a] / Pr [Y = 0|E = e, A = 0] does not
depend on e and is equal to h(a). The data follow a multiplicative survival model when there is no interaction between
A and E for Y = 0 on the multiplicative scale. A proof that Figure 8.13 represents a multiplicative survival model
proceeds as follows:
Pr [Y = 0|E = e, A = a] =
Pr [Y
O
= 0, Y
A
= 0, Y
E
= 0|E = e, A = a] = Pr[Y
O
= 0] Pr [Y
A
= 0|A = a] Pr [Y
E
= 0|E = e],
where the first equality is by determinism and the second by the DAG factorization.
Now set g(e) = Pr [Y
E
= 0|E = e] and h(a) = Pr[Y
O
= 0] Pr [Y
A
= 0|A = a]. Note if Pr [Y = 0|E = e, A = a] =
g(e)h(a), then Pr [Y = 1|E = e, A = a] = 1 −g(e)h(a) does not follow a multiplicative mortality model. Hence, when
A and E are conditionally independent given Y = 0, they will be conditionally dependent given Y = 1.
follow a multiplicative survival model (see Technical Point 8.2).
What is interesting about Figure 8.13 is that by adding the unmeasured
variables Y
A
, Y
E
and Y
O
, which functionally determine the observed variable
Y , we have created an augmented causal diagram that succeeds in representingAugmented causal DAGs, intro-
duced by Hern´an, Hern´andez-D´ıaz,
and Robins (2004), can be ex-
tended to represent the sufficient
causes described in Chapter 5 (Van-
derWeele and Robins, 2007c).
both the conditional independence between A and E given Y = 0 and the their
conditional dependence given Y = 1.
In summary, conditioning on a collider always induces an association be-
tween its causes, but this association could be restricted to certain levels of the
common effect. In other words, it is theoretically possible that selection on a
common effect does not result in selection bias when the analysis is restricted
to a single level of the common effect. Collider stratification is not always a
source of selection bias.
8.6 Selection without bias 117
Fine Point 8.2
The strength and direction of selection bias. We have referred to selection bias as an “all or nothing” issue: either
bias exists or it doesn’t. In practice, however, it is important to consider the expected direction and magnitude of the
bias.
The direction of the conditional association between 2 marginally independent causes A and E within strata of their
common effect Y depends on how the two causes A and E interact to cause Y . For example, suppose that, in the
presence of an undiscovered background factor U that is unassociated with A or E, having either A = 1 or E = 1 is
sufficient and necessary to cause death (an “or” mechanism), but that neither A nor E causes death in the absence
of U. Then among those who died (Y = 1), A and E will be negatively associated, because it is more likely that an
individual with A = 0 had E = 1 because the absence of A increases the chance that E was the cause of death. (Indeed,
the logarithm of the conditional odds ratio OR
AE|Y =1
will approach minus infinity as the population prevalence of U
approaches 1.0.) This “or” mechanism was the only explanation given in the main text for the conditional association
of independent causes within strata of a common effect; nonetheless, other possibilities exist.
For example, suppose that in the presence of the undiscovered background factor U , having both A = 1 and E = 1 is
sufficient and necessary to cause death (an “and” mechanism) and that neither A nor E causes death in the absence of
U. Then, among those who die, those with A = 1 are more likely to have E = 1, i.e., A and E are positively correlated.
A standard DAG such as that in Figure 8.12 fails to distinguish between the case of A and E interacting through an
“or” mechanism from the case of an “and” mechanism. Causal DAGs with sufficient causation structures (VanderWeele
and Robins, 2007c) overcome this shortcoming.
Regardless of the direction of selection bias, another key issue is its magnitude. Biases that are not large enough
to affect the conclusions of the study may be safely ignored in practice, whether the bias is upwards or downwards.
Generally speaking, a large selection bias requires strong associations between the collider and both treatment and
outcome. Greenland (2003) studied the magnitude of selection bias under the null, which he referred to as collider-
stratification bias, in several scenarios.
118 Selection bias
Chapter 9
MEASUREMENT BIAS AND “NONCAUSAL” DIAGRAMS
Suppose an investigator conducted a randomized experiment to answer the causal question “does one’s looking
up to the sky make other pedestrians look up too?” She found a weak association between her looking up and
other pedestrians’ looking up. Does this weak association reflect a weak causal effect? By definition of randomized
experiment, confounding bias is not expected in this study. In addition, no selection bias was expected because
all pedestrians’ responses—whether they did or did not look up—were recorded. However, there was another
problem: the investigator’s collaborator who was in charge of recording the pedestrians’ responses made many
mistakes. Specifically, the collaborator missed half of the instances in which a pedestrian looked up and recorded
these responses as “did not look up.” Thus, even if the treatment (the investigator’s looking up) truly had a strong
effect on the outcome (other people’s looking up), the misclassification of the outcome will result in a dilution of
the association between treatment and the (mismeasured) outcome.
We say that there is measurement bias when the association between treatment and outcome is weakened or
strengthened as a result of the process by which the study data are measured. Since measurement errors can occur
under any study design—including both randomized experiments and observational studies—measurement bias
need always be considered when interpreting effect estimates. This chapter provides a description of biases due to
measurement error.
9.1 Measurement error
In previous chapters we implicitly made the unrealistic assumption that all
variables were perfectly measured. Consider an observational study designed to
Figure 9.1
estimate the effect of a cholesterol-lowering drug A on the risk of liver disease Y .
We often expect that treatment A will be measured imperfectly. For example,
if the information on drug use is obtained by medical record abstraction, the
abstractor may make a mistake when transcribing the data, the physician may
forget to write down that the patient was prescribed the drug, or the patient
may not take the prescribed treatment. Thus, the treatment variable in our
analysis data set will not be the true use of the drug, but rather the measured
use of the drug. We will refer to the measured treatment as A
∗
(read A-star),
which will not necessarily equal the true treatment A for a given individual.
The psychological literature sometimes refers to A as the “construct” and to
A
∗
as the “measure” or “indicator.” The challenge in observational disciplines
is making inferences about the unobserved construct (e.g., cholesterol-lowering
drug use) by using data on the observed measure (e.g., information on statin
use from medical records).
The causal diagram in Figure 9.1 depicts the variables A, A
∗
, and Y . For
simplicity, we chose a setting with neither confounding nor selection bias for
the causal effect of A on Y . The true treatment A affects both the outcome Y
and the measured treatment A
∗
. The causal diagram also includes the node
U
A
to represent all factors other than A that determine the value of A
∗
. We
refer to the difference between an individual’s mismeasured value A
∗
and true
value A as the measurement error of A for that individual. The magnitude and
120 Measurement bias and “Noncausal” diagrams
Technical Point 9.1
Independence and nondifferentiality of measurement errors. For each individual, we define the measurement error
of A as the difference e
A
= A
∗
− A and the measurement error of Y as the difference e
Y
= Y
∗
− Y .
Let f(·) denote a probability density function (pdf). The measurement error e
A
of treatment and the measurement
error e
Y
of outcome are independent if their joint pdf equals the product of each marginal pdf, i.e., f(e
Y
, e
A
) =
f(e
Y
)f(e
A
). The measurement error e
A
of treatment is nondifferential if its pdf is independent of the outcome Y , i.e.,
f(e
A
|Y ) = f(e
A
). Analogously, the measurement error e
Y
of the outcome is nondifferential if its pdf is independent of
the treatment A, i.e., f(e
Y
|A) = f(e
Y
).
direction of the measurement error is determined by the factors in U
A
. NoteMeasurement error for discrete vari-
ables is known as misclassification. that including the node U
A
in the causal diagram is not strictly necessary
because U
A
is neither a cause shared by other variables on the diagram nor a
variable that is conditioned on. We include it, however, to provide an explicit
representation of the factors responsible for measurement error and for a direct
Figure 9.2
comparison with the causal diagrams that we will discuss next.
Besides treatment A, the outcome Y can be measured with error too. The
causal diagram in Figure 9.2 includes the measured outcome Y
∗
, and the factors
U
Y
responsible for the measurement error of Y . Figure 9.2 illustrates a common
situation in practice. One wants to compute the average causal effect of the
treatment A on the outcome Y , but these variables A and Y have not been, or
cannot be, measured correctly. Rather, only the mismeasured versions A
∗
and
Y
∗
are available to the investigator who aims at identifying the causal effect
of A on Y .
Figure 9.2 also represents a setting in which there is neither confounding
nor selection bias for the causal effect of treatment A on outcome Y . Ac-
cording to our reasoning in previous chapters, association is causation in this
setting. We can compute any A-Y association measure and endow it with a
Figure 9.3
causal interpretation as the effect of A on Y . For example, the associational
risk ratio Pr [Y = 1|A = 1] / Pr [Y = 1|A = 0] is equal to the causal risk ratio
Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
. Our implicit assumption in previous chapters,
which we now make explicit, was that perfectly measured data on A and Y
were available.
We now consider the more realistic setting in which only the mismea-
sured versions of treatment and outcome, A
∗
and Y
∗
, are available. Then
there is no guarantee that the measure of association between A
∗
and Y
∗
will
equal the measure of causal effect of A on Y . The associational risk ratio
Pr [Y
∗
= 1|A
∗
= 1] / Pr [Y
∗
= 1|A
∗
= 0] will generally differ from the causal
risk ratio Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
. We say that there is measurement
bias or information bias. In the presence of measurement bias, the identifia-
bility conditions of exchangeability, positivity, and consistency are insufficient
to compute the causal effect of treatment A on outcome Y .
9.2 The structure of measurement error
The causal structure of confounding can be summarized as the presence of
common causes of treatment and outcome, and the causal structure of selec-
tion bias can be summarized as conditioning on common effects of treatment
9.2 The structure of measurement error 121
and outcome (or of their causes). Measurement bias arises in the presence of
measurement error, but there is no single structure to summarize measurement
error. This section classifies the structure of measurement error according to
Figure 9.4
two properties—independence and nondifferentiality—that we describe below
(see Technical Point 9.1 for formal definitions).
The causal diagram in Figure 9.2 depicts the measurement errors U
A
and
U
Y
for both treatment A and outcome Y , respectively. According to the rules
of d-separation, the measurement errors U
A
and U
Y
are independent because
the path between them is blocked by colliders (either A
∗
or Y
∗
). Independent
measurement errors are expected to arise if, e.g., information on both drug
use A and liver toxicity Y was obtained from electronic medical records in
which data entry errors occurred haphazardly. In other settings, however, the
measurement errors for exposure and outcome may be dependent, as depicted
in Figure 9.3. For example, dependent measurement errors will occur if the
Figure 9.5
Figure 9.6
Figure 9.7
information were obtained retrospectively by phone interview and an individ-
ual’s ability to recall her medical history (U
AY
) affected the measurement of
both treatment A and outcome Y .
Figures 9.2 and 9.3 represent settings in which the factors U
A
responsible
for the measurement error of the treatment are independent of the true value
of the outcome Y , and the factors U
Y
responsible for the measurement error
for the outcome are independent of the true value of treatment A. We then say
that the measurement error for treatment is nondifferential with respect to the
outcome, and that the measurement error for the outcome is nondifferential
with respect to the treatment. The causal diagram in Figure 9.4 shows an
example of independent but differential measurement error in which the true
value of the outcome affects the measurement of the treatment (i.e., an arrow
from Y to U
A
). We now describe some examples of differential measurement
error of the treatment.
Suppose that the outcome Y was dementia rather than liver toxicity, and
that drug use A was ascertained by interviewing study participants. Since the
presence of dementia affects the ability to recall A, one would expect an arrow
from Y to U
A
. Similarly, one would expect an arrow from Y to U
A
in a study
to compute the effect of alcohol use during pregnancy A on birth defects Y
if alcohol intake is ascertained by recall after delivery—because recall may be
affected by the outcome of the pregnancy. The resulting measurement bias in
these two examples is often referred to as recall bias. A bias with the same
structure might arise if blood levels of drug A
∗
are used in place of actual drug
use A, and blood levels are measured after liver toxicity Y is present—because
liver toxicity affects the measured blood levels of the drug. The resulting
measurement bias is often referred to as reverse causation bias.
The causal diagram in Figure 9.5 shows an example of independent but
differential measurement error in which the true value of the treatment affects
the measurement of the outcome (i.e., an arrow from A to U
Y
). A differential
measurement error of the outcome will occur if physicians, suspecting that drug
use A causes liver toxicity Y , monitored patients receiving drug more closely
than other patients. Figures 9.6 and 9.7 depict measurement errors that are
both dependent and differential, which may result from a combination of the
settings described above.
In summary, we have discussed four types of measurement error: indepen-
dent nondifferential (Figure 9.2), dependent nondifferential (Figure 9.3), inde-
pendent differential (Figures 9.4 and 9.5), and dependent differential (Figures
9.6 and 9.7). The particular structure of the measurement error determines
the methods that can be used to correct for it. For example, there is a large
122 Measurement bias and “Noncausal” diagrams
Fine Point 9.1
The strength and direction of measurement bias. In general, measurement error will result in bias. A notable
exception is the setting in which A and Y are unassociated and the measurement error is independent and nondifferential:
If the arrow from A to Y did not exist in Figure 9.2, then both the A-Y association and the A
∗
-Y
∗
association would
be null. In all other circumstances, measurement bias may result in an A
∗
-Y
∗
association that is either further from
or closer to the null than the A-Y association. Worse, even under the independent and nondifferential measurement
error structure of Figure 9.2, non-extreme measurement bias may result in A
∗
-Y
∗
and A-Y trends in opposite directions
for non-dichotomous ordinal treatments and for continuous treatments. This trend reversal under independent and
nondifferential measurement error occurs when the conditional mean of A
∗
given A is a nonmonotonic function of A.
See Dosemeci, Wacholder, and Lubin (1990) and Weinberg, Umbach, and Greenland (1994) for details. VanderWeele
and Hern´an (2009) described a more general framework using signed causal diagrams.
The magnitude of the measurement bias depends on the magnitude of the measurement error. That is, measurement
bias generally increases with the strength of the arrows from U
A
to A
∗
and from U
Y
to Y
∗
. Causal diagrams do not
encode quantitative information, and therefore they cannot be used to describe the magnitude of the bias.
literature on methods for measurement error correction when the measurement
error is independent nondifferential. In general, methods for measurement er-
ror correction rely on a combination of modeling assumptions and validation
samples, i.e., subsets of the data in which key variables are measured with
little or no error. The description of methods for measurement error correc-
tion is beyond the scope of this book. Rather, our goal is to highlight that
the act of measuring variables (like that of selecting individuals) may intro-
duce bias (see Fine Point 9.1 for a discussion of its strength and direction).
Realistic causal diagrams need to simultaneously represent biases arising from
confounding, selection, and measurement. The best method to fight bias due
to mismeasurement is, obviously, to improve the measurement procedures for
the variables used in our analysis.
9.3 Mismeasured confounders and colliders
Besides the treatment A and the outcome Y , the confounders L may also be
measured with error. Mismeasurement of confounders may result in bias even
if both treatment and outcome are perfectly measured.
To see this, consider the causal diagram in Figure 9.8, which includes the
variables drug use A, liver disease Y , and history of hepatitis L. Individuals
with prior hepatitis L are less likely to be prescribed drug A and more likely
Figure 9.8
to develop liver disease Y . As discussed in Chapter 7, there is confounding
for the effect of the treatment A on the outcome Y because there exists an
open backdoor path A ← L → Y , but there is no unmeasured confounding
given L because the backdoor path A ← L → Y can be blocked by condition-
ing on L. That is, there is exchangeability of the treated and the untreated
conditional on the confounder L, and one can apply IP weighting or standard-
ization to compute the average causal effect of A on Y . The standardized, or
IP weighted, risk ratio based on L, Y , and A will equal the causal risk ratio
Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
.
Again the implicit assumption in the above reasoning is that the confounder
L was perfectly measured. Suppose investigators did not have access to the
9.3 Mismeasured confounders and colliders 123
study participants’ medical records. Rather, to ascertain previous diagnoses of
hepatitis, investigators had to ask participants via a questionnaire. Since not all
participants provided an accurate recollection of their medical history—some
did not want anyone to know about it, others had memory problems or simply
made a mistake when responding to the questionnaire—the confounder L was
measured with error. Note that Figure 9.8 does not explicitly represent the
factors U
L
responsible for the measurement error of L because the particular
structure of this error is not relevant to our discussion.
Investigators had data on the mismeasured variable L
∗
rather than on the
variable L. Unfortunately, the backdoor path A ← L → Y cannot be gener-
ally blocked by conditioning on L
∗
. The standardized (or IP weighted) risk
ratio based on L
∗
, Y , and A will generally differ from the causal risk ratio
Pr
Y
a=1
= 1
/ Pr
Y
a=0
= 1
. We then say that there is measurement bias
or information bias. The causal diagram in Figure 9.9 shows an example of
Figure 9.9
confounding of the causal effect of A on Y in which L is not the common cause
shared by A and Y . Here too mismeasurement of L leads to measurement bias
because the backdoor path A ← L ← U → Y cannot be generally blocked by
conditioning on L
∗
.
Alternatively, one could view the bias due to mismeasured confounders in
Figures 9.8 and 9.9 as a form of unmeasured confounding rather than as a form
of measurement bias. In fact the causal diagram in Figure 9.8 is equivalent
to that in Figure 7.8. One can think of L as an unmeasured variable and of
L
∗
as a surrogate confounder (see Fine Point 7.2). The particular choice of
terminology—unmeasured confounding versus bias due to mismeasurement of
the confounders—is irrelevant for practical purposes. In some settings, how-
ever, the use of mismeasured variables is sufficient to adjust for confounding.
See Fine Point 9.2 for some examples.
Mismeasurement of confounders may also result in apparent effect modi-
fication. As an example, suppose that all study participants who reported a
prior diagnosis of hepatitis (L
∗
= 1) and half of those who reported no prior
diagnosis of hepatitis (L
∗
= 0) did actually have a prior diagnosis of hepatitis
(L = 1). That is, the true and the measured value of the confounder coincide
in the stratum L
∗
= 1, but not in the stratum L
∗
= 0. Suppose further that
treatment A has no effect on any individual’s liver disease Y , i.e., the sharp
null hypothesis holds. When investigators restrict the analysis to the stratum
L
∗
= 1, there will be no confounding by L because all participants included
in the analysis have the same value of L (i.e., L = 1). Therefore they will
find no association between A and Y in the stratum L
∗
= 1. However, when
the investigators restrict the analysis to the stratum L
∗
= 0, there will be
confounding by L because the stratum L
∗
= 0 includes a mixture of individ-
uals with both L = 1 and L = 0. Thus the investigators will find a non-null
association between A and Y as a consequence of uncontrolled confounding
by L. If the investigators are unaware of the fact that there is mismeasure-
ment of the confounder in the stratum L
∗
= 0 but not in the stratum L
∗
= 1,
they could naively conclude that both the association measure in the stratum
L
∗
= 0 and the association measure in the stratum L
∗
= 1 can be interpreted
as effect measures. Because these two association measures are different, the
Figure 9.10
investigators will say that L
∗
is a modifier of the effect of A on Y even though
no effect modification by the true confounder L exists.
Finally, it is also possible that a collider C is measured with error. This
situation is represented in the causal diagram in Figure 9.10, which is equivalent
to Figure 8.2. When interested in the effect of A on Y under Figure 9.10,
conditioning on the mismeasured collider C
∗
will generally introduce selection
124 Measurement bias and “Noncausal” diagrams
Fine Point 9.2
When mismeasured confounders are not a problem. In many medical applications, measurement error in the
confounders does not introduce any bias. Suppose that high blood pressure L affects both the probability of receiving
antihypertensive therapy A and of having a stroke Y . Doctors and patients, however, do not make their treatment
decisions based on the true blood pressure L but based on the blood pressure measurement L
∗
that was recorded in the
doctor’s office. That is, L
∗
is the only information about blood pressure that is accessible to decision makers.
Figure 9.11 (which is structurally equivalent to Figure 7.2) represents this situation. The possibly mismeasured L
∗
fully mediates the effect of L on A because any component of L that was not captured by L
∗
remained unknown and
thus could not influence the decision to administer the treatment. It follows that the backdoor path between A and Y
can be blocked by conditioning on either the true L or the measured L
∗
. Therefore, it is irrelevant whether investigators
had access to the true L or to the measured L
∗
. Either variable is sufficient to adjust for confounding.
A more extreme example is shown in Figure 9.12. Under this causal diagram, having data on the true L is insufficient
to adjust for confounding whereas having data on the measured L
∗
is sufficient to adjust for confounding. The general
point is that effects can be identified whenever we have as much information in the data as the decision makers had to
make their decisions, regardless of whether that information resulted from perfectly measured variables or from variables
measured with error.
bias because C
∗
is a descendant of the collider and therefore a common effect
of the treatment A and the outcome Y .
9.4 Causal diagrams without mismeasured variables?
Figure 9.11
Figure 9.12
When drawing causal diagrams in previous chapters, we have been implicitly
making two simplifying, and related, assumptions. In this and the next section
we make those assumptions and their implications explicit.
The first assumption is that all variables on the diagram are perfectly mea-
sured. This assumption is not realistic because, in practice, measurement error
is often unavoidable for treatments, outcomes, confounders, and any other vari-
ables of interest. In this chapter, we have described how causal diagrams can be
used to represent mismeasured variables under different types of measurement
error. We have also explored the consequences of using the mismeasured vari-
ables, which are the only ones available to investigators, for the identification
of causal effects.
For example, suppose that we are interested in the effect of the treatment
A on the outcome Y , but we only have data on the measured treatment A
∗
and the measured outcome Y
∗
. We have seen how measurement error of treat-
ment or outcome may induce a noncausal association between the measured
treatment A
∗
and the measured outcome Y
∗
, even if treatment A has a null
effect on the outcome Y and even if there is no confounding and no selection
bias. Also, in the presence of confounding, we have seen how measurement
error of a confounder may prevent the measured confounder L
∗
from blocking
a backdoor path that would be successfully blocked if we had access to the
true confounder L.
Because all variables can be expected to be measured with some error, it
might be argued that a causal diagram should always represent both true and
measured values of all its variables. Yet, in many settings, the magnitude of
the measurement error may be judged, or known, to be too small to matter. In
9.5 Many proposed causal diagrams include noncausal arrows 125
those settings, a causal DAG that makes no distinction between measured and
true values of a variable may be preferable for simplicity. If confounding and
selection bias exist under perfect measurement of all variables, then these biases
will typically exist under measurement error too (though exceptions exist as
shown in Fine Point 9.2). Drawing causal diagrams without measurement error
allows us to focus on confounding and selection bias without being distracted
by measurement issues.
Considering causal diagrams without measurement error is often a helpful
first approximation. Once we have a good understanding of possible biases
under perfect measurement, we can add measurement error as an additional
layer of complexity. This 2-step approach to the drawing of causal diagrams
helps us isolate the study of two sources of bias—confounding and selection—
without being overburdened by the third one—measurement. We follow this
approach in the book: when the emphasis is on confounding and selection bias,
we omit the distinction between true and measured values of the variables on
the causal diagram.
The second assumption we have made so far, also related to measurement, is
a fundamental assumption in any causal diagram. We discuss this assumption
in the next section.
9.5 Many proposed causal diagrams include noncausal arrows
Consider the causal diagram in Figure 9.13 (which is equal to Figure 7.1). Let
A, Y , and L be three binary variables representing an antiviral treatment given
to patients with COVID-19, death, and obesity (defined as body mass index
greater than 30), respectively. Patients with obesity are more likely to receive
Figure 9.13
treatment and to be hospitalized in the absence of treatment. Therefore, ex-
perts draw a DAG with arrows from L into both A and Y . For simplicity, we
will assume that the decision to give treatment is only influenced by L and
by the physician’s preference, which is unrelated to any other variables on the
diagram. Also for simplicity, we assume no measurement error for any variable.
Specifically, the true value of L equals its measured value L
∗
so the latter does
not need be included on the diagram.
We have previously discussed how, in causal diagrams, treatment nodes
have a different status than other nodes (see Section 6.4). The reason is that
meaningful quantitative causal inference about the effect of treatment A on
outcome Y requires well-defined, actual or hypothetical, interventions on A.
Otherwise the counterfactual outcomes Y
a
remain undefined and cannot be
linked to the observed outcomes Y , i.e., the consistency condition does not hold
(see Chapter 3). In our example, the intervention represented by treatment A is
well-defined because we have a good understanding of how antiviral treatment
can be administered or withheld. Thus, the presence or absence of an arrow
from A to Y is well defined too.
We now extend our discussion to nodes that are not considered a treatment,
such as obesity L in Figure 9.13. As we discussed extensively in Chapter 3,
interventions on obesity L on death are not well defined. Thus, the counter-
factual outcomes Y
l
remain undefined.
So far in this book we have ignored this problem, but many DAGs pro-
posed in the health and social sciences have arrows emanating from variables
for which well-defined interventions do not exist, like L in Figure 9.13. Those
arrows, like the arrow L → Y in Figure 9.13, do not have a causal interpreta-
126 Measurement bias and “Noncausal” diagrams
Fine Point 9.3
Whether interventions are well-defined depends on the outcome of interest. In the main text we said that there
may exist well-defined interventions for the effect of L on A even if there are no well-defined interventions for the effect
of L on Y . This statement needs a better explanation because, if we truly knew how to intervene on L to study its
effect on A, then what would prevent us from using the same intervention to study its effect on Y ?
This apparent contradiction results from an abuse of notation. In our example, we used the symbol L to refer to
two concepts: (i) the physical quantity body weight (measured in kilos), and (ii) the recorded value of that quantity
(measured in kilos). In a world without measurement error, both (i) and (ii) have the same numerical value and
thus conflating both concepts has no practical impact. However, when we described in the main text a well-defined
intervention for L on A, we were referring to an intervention on (ii) rather than on (i), and thus a distinction between
both concepts is warranted.
Let us use the symbol L to depict the physical quantity “body weight”, and the symbol L
∗
to depict the recording
of L. If we add L
∗
to the causal DAG, there would be a deterministic arrow from L to L
∗
(assuming no measurement
error) and a regular arrow from L
∗
to A. According to this expanded causal DAG, body weight L only affects treatment
A when the doctor learns the value L
∗
. Therefore, if we intervene on the recorded value L
∗
, even if we leave the
physical quantity L unchanged, the doctors’ behavior would be the same as if we could somehow intervene on L. It is
in this sense that we say in the main text that there are well-defined interventions on L when the outcome is A—the
counterfactuals A
l
are well defined—but not when the outcome is Y —the counterfactuals Y
l
are not well defined.
tion. To explore the consequences of using these DAGs with noncausal arrows,
we now discuss Figure 9.13 in more detail. Let us consider separately the
arrows L → A and L → Y .
When experts drew the arrow from L → A, they were appropriately using
their subject-matter knowledge. Experts knew that doctors are more likely
to administer treatment to obese patients upon learning that they are obese.
One could imagine well-defined interventions for the effect of L on A, such as
presenting the treating physician with a patient whose body mass index differs
from that of the patient for whom the treatment decision is being made. There-
fore, drawing the arrow from L → A is reasonable. For additional discussion
on this point, see Fine Point 9.3 after reading the next paragraph.
Were the experts justified in drawing the arrow L → Y ? Suppose the
experts know that obese patients are more likely to die, but cannot propose
well-defined interventions for the effect of L and Y . Then the arrow L → Y
has no causal interpretation. In this chapter and generally throughout the
book, we restrict the term causal DAG to DAGs for which all arrows have
a well-defined causal interpretation. Therefore, under our restriction and the
current state of knowledge, Figure 9.13 is a “noncausal” diagram. We have
placed the word “noncausal” in quotes as a reminder that many papers in
the causal literature continue to define DAGs that include both causal and
noncausal arrows as causal diagrams. See Fine Point 9.4 for more discussion
on “noncausal” diagrams.
Figure 9.14
Now suppose that a second group of experts proposes an alternative in-
terpretation for the known fact that “obese patients are more likely to die”:
obesity is a surrogate or proxy for a hidden factor H that has a causal effect
on Y . The corresponding causal diagram is Figure 9.14 (structurally identical
to Figure 7.2), which includes unmeasured and possibly unknown variables H
such as genetic factors, metabolic factors related to body fat stores, microbiota,
and probably others not yet discovered by science. According to Figure 9.14,
the effect of the factors H on the treatment A is fully mediated through L.
9.5 Many proposed causal diagrams include noncausal arrows 127
Fine Point 9.4
“Noncausal”diagrams with well-defined statistical interpretations. Consider a DAG representation for an FFR-
CISTG model that assumed (i) the treatment A was the only variable with well-defined interventions with counterfactuals
(M
a
, Y
a
) and (ii) the distribution of the variables on the DAG factored according to the DAG, i.e., each variable was
conditionally independent of its non-descendants given its parents. In these DAGs, the arrows do not, in general, have a
causal interpretation. Rather, the arrows simply encode, via d-separation, the conditional independencies satisfied by the
variables on the diagram and on the associated SWIG (see Technical Point 21.12). Under this noncausal interpretation
of DAGs, the L → Y arrow need not be removed in Figure 9.13 just because interventions on L are not well-defined.
Richardson and Robins (2013) pointed out serious difficulties with this approach. Specifically, if arrows have no
causal interpretation, then there is no reason to expect the distribution of the study variables to be representable by
(i.e., factor according to) any (incomplete) DAG. This difficulty is magnified in the presence of unmeasured variables U
because then it is not even possible to empirically check some conditional independencies from the observed data. For
example, the front door graph of Figure 7.14 implies that Y is independent of A given M and U. Any investigator who
chooses Figure 7.14 as the appropriate causal DAG must have had substantive reasons for postulating this conditional
independence. Indeed many researchers might find it hard to imagine what those reasons could be other than the belief
that A and Y share a common cause U and that the causal effect of A on Y is completely mediated by M—a belief
that endows every arrow on the diagram with a causal interpretation. See also Fine Point 9.5.
One can alternatively view the use of noncausal arrows as a response by researchers who are skeptical of the strong
causal claim that M-counterfactuals Y
m
exist. This “noncausal” approach interprets Figure 7.14 as representing the
hypothesized statistical independence Y ⊥⊥A|M among the observed variables that would hold in a future trial in which
A is randomly assigned. Thus, if this independence fails to hold in the future trial, the justification of the strong causal
claim that M-counterfactuals exist has been falsified along with the structure in Figure 7.14.
That is, there is no direct arrow from H to A. This assumption is reasonable if,
for example, the only information used to make real world treatment decisions
is obesity L.
Like Figure 9.13, Figure 9.14 encodes the (reasonable) assumptions that
there are well-defined interventions for the effect of obesity L on treatment
A—this assumption is represented by the arrow L → A—and that there is no
direct effect of L on Y not through A. Therefore, the associated counterfactuals
are A
l
and Y
a
, which imply the existence of a well-defined intervention of L on
Y with Y
l
= Y
A
l
. That is, Y
l
is equal to Y
a
for a equal to the counterfactual
A
l
. In the language of Technical Point 6.2, we say that Y
l
is obtained from
Y
a
and A
l
by recursive substitution. Note there is no contradiction in Y
l
being well-defined for the causal diagram of Figure 19.14 but not for Figure
9.13 because, assuming Figure 9.14 is a causal diagram, Figure 9.13 is not, as
Figure 9.13 fails to include the common cause H of L and Y . See also Fine
Point 9.6.
Figure 9.14 also encodes the assumption that well-defined interventions ex-
ist for the effect of the unknown factors H on both L and Y . That is, the
arrows H → L and H → Y on Figure 9.14 imply that there exist counter-
factuals L
h
and Y
h
, respectively, associated with a well-defined intervention
on H. It may seem counterintuitive for us to stipulate simultaneously that (i)
the current state of knowledge is insufficient to even characterize many of the
factors in H, and (ii) well-defined interventions exist for the effect of H on
both L and Y . To explain why we might do so and hence regard Figure 9.14
as a causal diagram under the current state of knowledge, let us define H more
precisely.
When, as in Figure 9.13, there exists a variable L on a proposed causal
128 Measurement bias and “Noncausal” diagrams
Fine Point 9.5
A connection to the front door formula. Figure 9.14 is precisely the front door diagram in Figure 7.14 with L → A
substituted for A → M. Hence E
Y
l
is identified by the front door formula in Technical Point 7.4 with L, l, l
′
substituted for A, a, a
′
and A, a substituted for M, m.
Suppose a researcher modifies Figure 9.14 by adding a direct L → Y arrow. The justification is that, when dietitians
and physical therapists are referred an individual who has a high value of L, they provide additional ancillary care (such
as dietary advice, exercises to prevent deep vein thrombosis, etc.), which is not recorded in the medical record available
to the researchers. The counterfactual variable Y
l
in the unmodified diagram in Figure 9.14 differs from the variable Y
l
in the modified diagram with a direct L → Y arrow. In the unmodified graph Y
l
− Y
l
′
is the causal effect of l versus
l
′
via the causal pathway L → A → Y . In contrast, in the modified graph, Y
l
− Y
l
′
is the total effect along the two
pathways L → Y and L → A → Y . In fact, in contrast to the unmodified graph, E
Y
l
is not identified under the
modified graph.
One might conjecture that the effect of l versus l
′
along the pathway L → A → Y should be the same in the two
graphs and thus remain identified by the front door formula. This conjecture is indeed true, although we must defer a
proof until we study the identification of path-specific effects in Chapter 23.
diagram for which Y
l
is ill-defined, we introduce a high-dimensional parent H
of L that encodes all unmeasured—known and unknown—causal determinants
of L (other than any known, but unmeasured, variables U already present on
the diagram). H may be a direct cause and thus a parent of other variables
such as Y as well. We regard L as the lower-dimensional effect of, or surrogate
for, H that has been recorded for data analysis. For example, in our obesity
example, the continuous variable body mass index L is an effect of the largely
unknown factors H that regulate body weight. In some instances, L may be
thought of as a deterministic (many to one) function of H.
Even though we are ignorant of the precise intervention on the components
(many unknown) of H that affect Y , we nonetheless assume that there exist
factors H that have a causal effect on Y . Because current knowledge does not
rule out the existence of well-defined interventions for the effect of H on Y ,
the arrow H → Y is tentatively justified and therefore we consider Figure 9.14
to be a causal diagram.
Note that, for clarity, in this section we distinguished between H, unmea-
sured common causes between two variables when the effect of one of the
variables on the other is ill-defined, from U, unmeasured common causes be-
tween two variables when the effect of one of the variables on the other is
well-defined. In most of the book, we do not make this distinction and simply
use U to represent all unmeasured variables.
9.6 Does it matter that many proposed diagrams include noncausal arrows?
We have seen that the original DAG (Figure 9.13) proposed by the experts is
not a causal DAG because one of its arrows (the one from L to Y ) cannot be
causally interpreted. Yet, despite being causally wrong, this DAG is adequate
for causal inference about the effect of treatment A on the outcome Y : regard-
less of whether we use the noncausal DAG in Figure 9.13 or the causal DAG in
Figure 9.14, we conclude that all backdoor paths between A and Y are blocked
by conditioning on L.
9.6 Does it matter that many proposed diagrams include noncausal arrows? 129
Thus the DAG in Figure 9.13, which lacks the node U and includes the non-
causal arrow L → Y , correctly guides data analysis because adjusting for L is
all that is needed in the identifying formula—standardization or IP weighting
in our example—for the average causal effect of A on Y . This conclusion is
expected because, in both DAGs, there are no arrows from unmeasured vari-
ables into treatment A (see also Fine Point 9.2). This oversimplified scenario
illustrates a general issue: in realistic complex settings, expert knowledge is
rarely good enough to draw a causal diagram in which all of its components
are known.
Figure 9.15
Figure 9.16
In fact, many DAGs proposed in the health and social sciences are actually
noncausal DAGs because they lack the hidden variables H that make the DAG
causal. By including a variable without well-defined interventions for its effect
on its descendants (like obesity and its descendant death), we are effectively
declaring that our DAG is noncausal. It is, however, possible that the identify-
ing formula for the causal effect of interest is the same when derived from the
noncausal DAG and from the causal DAG with hidden nodes. This is exactly
what happened in our example: if Figure 9.14 is the correct DAG, using the
DAG in Figure 9.13 will result in the same identifying formula.
But noncausal DAGs may be misleading. Consider the DAG in Figure 9.15.
Declaring that this DAG is a causal DAG implies that we believe there are well-
defined interventions for the effect of L on Y (because there is a direct arrow
from L to Y ). Conversely, in the absence of such well-defined interventions,
the DAG is noncausal and we can only hope that the identifying formula based
on L happens to be correct.
Following our reasoning above, Figure 9.16 depicts our measured variable
L is actually a surrogate of an unknown variable H for which well-defined
interventions exist. In Figure 9.15 the backdoor path between A and Y is
blocked by L, but in Figure 9.16 it is not.
Therefore, if investigators unaware of the status of their measured variable
as a surrogate confounder L proposed Figure 9.15 instead of Figure 9.16, they
would reach the incorrect conclusion that L is sufficient to block all backdoor
paths, as discussed in Section 9.3. When drawing causal DAGs, we need to
think carefully whether the variables that happen to be measured are also the
variables for which well-defined interventions exist. Otherwise, lack of attention
to the noncausal arrows of a DAG may give us false confidence in the validity
of our effect estimates. See Fine Point 9.6 for another example.
Figure 9.17
Figure 9.18
We have come a long way since we introduced causal diagrams in Chapter
6. Causal DAGs and SWIGs are formidable tools for investigators to organize
and communicate their causal assumptions but, as we have seen in this chapter,
these diagrams are subject to the same practical constraints that are inherent
to causal inference in general. Specifically, a causal arrow X → Y cannot be
meaningfully interpreted in the absence of well-defined interventions for the
effect of X on Y .
When proposing a causal DAG, we need to think carefully about the inter-
pretation of each of its arrows. A scientifically blind acceptance of DAGs with
noncausal arrows may lead to incorrect conclusions for causal inference. This
level of scrutiny is unnecessary for causal diagrams representing an electrical
circuit in which all interventions are well-defined, but indispensable for the
causal diagrams proposed in the health and social sciences.
The above discussion simplifies the concept of well-defined intervention for
pedagogic purposes. As discussed in Chapter 3, no intervention is perfectly
130 Measurement bias and “Noncausal” diagrams
Fine Point 9.6
From noncausal diagrams to causal diagrams. Suppose some investigators interested in the effect of A on Y
proposed the DAG in Figure 9.17. To draw this DAG, they relied on prior knowledge about the temporal order of the
variables and the following two facts: (i) the measured variable L is associated with Y , and (ii) there is one set of
unmeasured, but known, factors U that affect A and are associated with L. As discussed in Fine Point 7.4, the effect
of A on Y is not identifiable if Figure 9.17 is the true causal diagram because L is a descendant of A.
Upon further reflection, the investigators realize that there are no well-defined interventions for the effect of L on Y .
Therefore, the arrow L → Y is not a causal arrow and their DAG is not causal. To transform Figure 9.17 into a causal
diagram, they add the hidden variable H with a causal arrow into Y and represent L as a surrogate of H. Figure 9.18
depicts their revised DAG. The effect of A on Y is not identifiable if Figure 9.18 is the true causal diagram because the
backdoor path A ← U → H → Y cannot be blocked by any measured variable.
Note that the investigators kept the arrow U → A, which implies that they believe that there are well-defined
interventions for the effect of U and A. They also redirected the arrows from U and A to L in Figure 9.17 towards H
in Figure 9.18. This implies that the investigators believe that there must exist well-defined interventions for the effect
of both U and A on H and that the effects of both U and A on L are fully mediated by their effect on H. (Even if
L were a deterministic function of H, which is compatible with Figure 9.18, conditioning on L would not block paths
through H because H is not a deterministic function of L, as it is of higher dimensionality and complexity than L.)
The inheritance by H in Figure 9.18 of all the arrows into L in Figure 9.17 is not always warranted. For example, U
may have direct effect on L as in the causal DAG in Figure 9.19 rather than on H as in Figure 9.18. If, in fact, Figure
9.19 is the true causal DAG then the effect of A on Y would be identifiable because there are no open backdoor paths
between A and Y . Note that, in Figure 19.9, the surrogate L cannot be a deterministic function of H as it is also
affected by U. An example where, as in Figure 9.19, U has a direct effect on the surrogate L but no direct effect on H
is the following: U denotes a physician’s decision to order a particular diagnostic test, L the result of the test, and H
the underlying biological determinants of the test result.
well-defined but, for some interventions, the scientific consensus is that they
Figure 9.19
are sufficiently well-defined. We have argued that quantitative causal inference
fundamentally relies on the (admittedly fuzzy) concept of sufficiently well-
defined interventions. Therefore, in the remainder of this book, except for
several well sign-posted exceptions, we will assume all DAGs are strictly causal
in the sense that every arrow on the DAG represents a sufficiently well-defined
intervention. That is, each arrow is associated with an intervention that can
be specified in such a way that no meaningful vagueness remains based on
current scientific knowledge. In a few years or decades, we may find out that
our beliefs, and thus our causal diagrams, were incorrect.
Chapter 10
RANDOM VARIABILITY
Suppose an investigator conducted a randomized experiment to answer the causal question “does one’s looking
up to the sky make other pedestrians look up too?” She found an association between her looking up and other
pedestrians’ looking up. Does this association reflect a causal effect? By definition of randomized experiment,
confounding bias is not expected in this study. In addition, no selection bias was expected because all pedestrians’
responses—whether they did or did not look up—were recorded, and no measurement bias was expected because
all variables were perfectly measured. However, there was another problem: the study included only 4 pedestrians,
2 in each treatment group. By chance, 1 of the 2 pedestrians in the “looking up” group, and neither of the 2
pedestrians in the “looking straight” group, was blind. Thus, even if the treatment (the investigator’s looking
up) truly had a strong average effect on the outcome (other people’s looking up), half of the individuals in the
treatment group happened to be immune to the treatment. The small size of the study population led to a dilution
of the estimated effect of treatment on the outcome.
There are two qualitatively different reasons why causal inferences may be wrong: systematic bias and random
variability. The previous three chapters described three types of systematic biases: selection bias, measure-
ment bias—both of which may arise in observational studies and in randomized experiments—and unmeasured
confounding—which is not expected in randomized experiments. So far we have disregarded the possibility of
bias due to random variability by restricting our discussion to huge study populations. In other words, we have
operated as if the only obstacles to identify the causal effect were confounding, selection, and measurement. It is
about time to get real: the size of study populations in etiologic research rarely precludes the possibility of bias
due to random variability. This chapter discusses random variability and how we deal with it.
10.1 Identification versus estimation
The first nine chapters of this book are concerned with the computation of
causal effects in study populations of near infinite size. For example, when
computing the causal effect of heart transplant on mortality in Chapter 2, we
only had a twenty-person study population but we regarded each individual
in our study as representing 1 billion identical individuals. By acting as if
we could obtain an unlimited number of individuals for our studies, we could
ignore random fluctuations and could focus our attention on systematic biases
due to confounding, selection, and measurement. Statisticians have a name for
problems in which we can assume the size of the study population is effectively
infinite: identification problems.
Thus far we have reduced causal inference to an identification problem. Our
only goal has been to identify (or, as we often said, to compute) the average
causal effect of treatment A on the outcome Y . The concept of identifiability
was first described in Section 3.1—and later discussed in Sections 7.2 and
8.4—where we also introduced some conditions generally required to identify
causal effects even if the size of the study population could be made arbitrarily
large. These so-called identifying conditions were exchangeability, positivity,
and consistency.
Our ignoring random variability may have been pedagogically convenient
to introduce systematic biases, but also extremely unrealistic. In real research
132 Random variability
projects, the study population is not effectively infinite and hence we cannot
ignore the possibility of random variability. To this end let us return to our
twenty-person study of heart transplant and mortality in which 7 of the 13
treated individuals died.
Suppose our study population of 20 can be conceptualized as being a ran-
dom sample from a super-population so large compared with the study popu-
lation that we can effectively regard it as infinite. Further, suppose our goal is
to make inferences about the super-population. For example, we may want
to make inferences about the super-population probability (or proportion)
Pr[Y = 1|A = a]. We refer to the parameter of interest in the super-population,
the probability Pr[Y = 1|A = a] in this case, as the estimand. An estimator
is a rule that takes the data from any sample from the super-population and
produces a numerical value for the estimand. This numerical value for a par-
ticular sample is the estimate from that sample. The sample proportion of
individuals that develop the outcome among those receiving treatment level
a,
c
Pr[Y = 1 | A = a], is an estimator of the super-population probability
Pr[Y = 1|A = a]. The estimate from our sample is
c
Pr[Y = 1 | A = a] = 7/13.
More specifically, we say that 7/13 is a point estimate. The value of the esti-
mate will depend on the particular 20 individuals randomly sampled from the
super-population.
As informally defined in Chapter 1, an estimator is consistent for a par-
ticular estimand if the estimates get (arbitrarily) closer to the parameter as
the sample size increases (see Technical Point 10.1 for the formal definition).
Thus the sample proportion
c
Pr[Y = 1 | A = a] consistently estimates the
super-population probability Pr[Y = 1|A = a], i.e., the larger the num-
ber n of individuals in our study population, the smaller the magnitude of
Pr[Y = 1|A = a] −
c
Pr[Y = 1 | A = a] is expected to be. Previous chap-
ters were exclusively concerned with identification; from now on we will be
concerned with statistical estimation.For an introduction to statistics,
see the book by Wasserman (2004).
For a more detailed introduction,
see Casella and Berger (2002).
Even consistent estimators may result in point estimates that are far from
the super-population value. Large differences between the point estimate and
the super-population value of a proportion are much more likely to happen
when the size of the study population is small compared with that of the super-
population. Therefore it makes sense to have more confidence in estimates
that originate from larger study populations. In the absence of systematic
biases, statistical theory allows one to quantify this confidence in the form of a
confidence interval around the point estimate. The larger the size of the study
population, the narrower the confidence interval. A common way to construct
a 95% confidence interval for a point estimate is to use a 95% Wald confidence
interval centered at a point estimate. It is computed as follows.
First, estimate the standard error of the point estimate under the assump-
tion that our study population is a random sample from a much larger super-
population. Second, calculate the upper limit of the 95% Wald confidence
interval by adding 1.96 times the estimated standard error to the point esti-
mate, and the lower limit of the 95% confidence interval by subtracting 1.96
times the estimated standard error from the point estimate. For example, con-
sider our estimator
c
Pr[Y = 1 | A = a] = ˆp of the super-population parameter
Pr[Y = 1|A = a] = p. Its standard error is
q
p(1−p)
n
(the standard error of a
binomial) and thus its estimated standard error is
q
ˆp(1−ˆp)
n
=
q
(7/13)(6/13)
13
=
0.138. Recall that the Wald 95% confidence interval for a parameter θ based
on an estimator
b
θ is
b
θ ±1.96 × bse
b
θ
where bse
b
θ
is an estimate of the (exact
10.1 Identification versus estimation 133
or large sample) standard error of
b
θ and 1.96 is the upper 97.5% quantile of
a standard normal distribution with mean 0 and variance 1. Therefore the
95% Wald confidence interval for our estimate is 0.27 to 0.81. The length and
centering of the 95% Wald confidence interval will vary from sample to sample.
A 95% confidence interval is calibrated if the estimand is contained in theA Wald confidence interval cen-
tered at ˆp is only guaranteed to be
valid in large samples. For simplic-
ity, here we assume that our sample
size is sufficiently large for the va-
lidity of our Wald interval.
interval in 95% of random samples, conservative if the estimand is contained in
more than 95% of samples, and anticonservative otherwise. We will say that a
confidence interval is valid if, for any value of the true parameter, the interval
is either calibrated or conservative, i.e. it covers the true parameter at least
95% of the time. We would like to choose the valid interval whose width is
narrowest.
The validity of confidence intervals is defined in terms of the frequency of
coverage in repeated samples from the super-population, but we only see one
of those samples when we conduct a study. Why should we care about what
would have happened in other samples that we did not see? One important
answer is that the definition of confidence interval also implies the following.
Suppose we and all of our colleagues keep conducting research studies for the
rest of our lifetimes. In each new study, we construct a valid 95% confidence
interval for the parameter of interest. Then, at the end of our lives, we can look
back at all the studies that were conducted, and conclude that the parameters
of interest were trapped in—or covered by—the confidence interval in at least
95% of the studies. Unfortunately, we will have no way of identifying the (up
to) 5% of the studies in which the confidence interval failed to include the
super-population quantity.
Importantly, the 95% confidence interval from a single study does not im-
ply that there is a 95% probability that the estimand is in the interval. In
our example, we cannot conclude that the probability that the estimand lies
between the values 0.27 and 0.81 is 95%. The estimand is fixed, which implies
that either it is or it is not included in the particular interval (0.27, 0.81).
In this sense, the probability that the estimand is included in that interval is
either 0 or 1. A confidence interval only has a frequentist interpretation. Its
level (e.g., 95%) refers to the frequency with which the interval will trap theIn contrast with a frequentist 95%
confidence interval, a Bayesian 95%
credible interval can be interpreted
as “there is a 95% probability that
the estimand is in the interval”.
However, for a Bayesian, probabil-
ity is defined not as a frequency
over hypothetical repetitions but as
degree-of-belief. In this book we
adopt the frequency definition of
probability. See Fine Point 11.2 for
more on Bayesian intervals.
unknown super-population quantity of interest over a collection of studies (or
in hypothetical repetitions of a particular study).
Confidence intervals are often classified as either small-sample or large-
sample confidence intervals. A small-sample valid (conservative or calibrated)
confidence interval is one that is valid at all sample sizes for which it is de-
fined. Small-sample calibrated confidence intervals are sometimes called ex-
act confidence intervals. A large-sample (equivalently, asymptotic) valid con-
fidence interval is one that is valid only in large samples. A large-sample
calibrated 95% confidence interval is one whose coverage becomes arbitrarily
close to 95% as the sample size increases. The Wald confidence interval for
Pr[Y = 1|A = a] = p mentioned above is a large-sample calibrated confidence
interval, but not a small-sample valid interval. (There do exist small-sample
valid confidence intervals for p, but they are not often used in practice.) WhenThere are many valid large-sample
confidence intervals other than the
Wald interval (Casella and Berger,
2002). One of these might be pre-
ferred over the Wald interval, which
can be badly anti-conservative in
small samples (Brown et al, 2001).
the sample size is small, a valid large-sample confidence interval, such as the
Wald 95% confidence interval of our example above, may not be valid. In this
book, when we use the term 95% confidence interval, we mean a large-sample
valid confidence interval, like a Wald interval, unless stated otherwise. See also
Fine Point 10.1.
However, not all consistent estimators can be used to center a valid Wald
confidence interval, even in large samples. Most users of statistics will consider
an estimator unbiased if it can center a valid Wald interval and biased if it
134 Random variability
Fine Point 10.1
Honest confidence intervals. The smallest sample size at which a large-sample, valid 95% confidence interval covers
the true parameter at least 95% of the time may depend on the unknown value of the true parameter. We say a
large-sample valid 95% confidence interval is uniform or honest if there exists a sample size n at which the interval is
guaranteed to cover the true parameter value at least 95% of the time, whatever be the value of the true parameter. We
demand honest intervals because, in the absence of uniformity, at any finite sample size there may be data generating
distributions under which the coverage of the true parameter is much less than 95%. Unfortunately, for a large-sample,
honest confidence interval, the smallest such n is generally unknown and is difficult to determine even by simulation.
See Robins and Ritov (1997) for technical details.
In the remainder of the text, when we refer to valid confidence intervals, we will mean large-sample honest confidence
intervals. By definition, any small-sample valid confidence interval is uniform or honest for all n for which the interval
is defined.
cannot (see Technical Point 10.1 for details). For now, we will equate the term
bias with the inability to center valid Wald confidence intervals. Also, bear in
mind that confidence intervals only quantify uncertainty due to random error,
and thus the confidence we put on confidence intervals may be excessive in the
presence of systematic biases (see Fine Point 10.2 for details).
10.2 Estimation of causal effects
Suppose our heart transplant study was a marginally randomized experiment,
and that the 20 individuals were a random sample of all individuals in a nearly
infinite super-population of interest. Suppose further that all individuals in
the super-population were randomly assigned to either A = 1 or A = 0, and
that all of them adhered to their assigned treatment. Exchangeability of the
treated and the untreated would hold in the super-population, i.e., Pr[Y
a
=
1] = Pr[Y = 1|A = a], and therefore the causal risk difference Pr[Y
a=1
= 1] −
Pr[Y
a=0
= 1] equals the associational risk difference Pr[Y = 1|A = 1]−Pr[Y =
1|A = 0] in the super-population.
Because our study population is a random sample of the super-population,
the sample proportion of individuals that develop the outcome among those
with observed treatment value A = a,
c
Pr[Y = 1 | A = a], is an unbiased
estimator of the super-population probability Pr[Y = 1|A = a]. Because of
exchangeability in the super-population, the sample proportion
c
Pr[Y = 1 | A =
a] is also an unbiased estimator of Pr[Y
a
= 1]. Thus, traditional statistical
“testing”of the causal null hypothesis Pr[Y
a=1
= 1] = Pr[Y
a=0
= 1] boils
down to comparing the sample proportions
c
Pr [Y = 1 | A = 1] = 7/13 and
c
Pr [Y = 1 | A = 0] = 3/7. Standard statistical methods can also be used to
compute 95% confidence intervals for the causal risk difference and causal
risk ratio in the super-population, which are estimated by (7/13) − (3/7) and
(7/13)/(3/7), respectively. Slightly more involved, but standard, statistical
procedures are used in observational studies to obtain confidence intervals for
standardized, IP weighted, or stratified association measures.
There is an alternative way to think about sampling variability in random-
ized experiments. Suppose only individuals in the study population, not all
individuals in the super-population, are randomly assigned to either A = 1
10.2 Estimation of causal effects 135
Technical Point 10.1
Bias and consistency in statistical inference. We have discussed systematic bias (due to unknown sources of
confounding, selection, or measurement error) and consistent estimators in earlier chapters. Here we discuss these and
other concepts of bias, and describe how they are related.
To provide a formal definition of consistent estimator for an estimand θ, suppose we observe n independent, identically
distributed (i.i.d.) copies of a vector-valued random variable whose distribution P lies in a set M of distributions (our
model). Then the estimator
b
θ
n
is consistent for θ = θ (P ) in model M if
b
θ
n
converges to θ in probability for every
P ∈ M i.e.
Pr
P
h
|
b
θ
n
− θ (P ) | > ε
i
→ 0 as n → ∞ for every ε > 0, P ∈ M.
The estimator
b
θ
n
is exactly unbiased in model M if, for every P ∈ M, E
P
h
b
θ
n
i
= θ (P ). The exact bias under P is
the difference E
P
h
b
θ
n
i
−θ (P ). We denote the estimator by
b
θ
n
rather than by simply
b
θ to emphasize that the estimate
depends on the sample size n. On the other hand, the parameter θ (P ) is a fixed, though unknown, quantity depending
on P ∈ M. When P is the distribution generating the data in our study, we often suppress the P in the notation and
write E
h
b
θ
n
i
= θ. For many parameters θ, such as the risk ratio Pr[Y = 1|A = 1]/ Pr[Y = 1|A = 0], exactly unbiased
estimators do not exist.
A systematically biased estimator is neither consistent nor exactly unbiased. Robins and Morgenstern (1987) argue
that most applied researchers (e.g., epidemiologists) will declare an estimator unbiased only if it can center a valid Wald
confidence interval. They show that under this definition, an estimator is only unbiased if it is uniformly asymptotic
normal and unbiased (UANU), as only UANU estimators can center valid standard Wald intervals for θ (P ) under
the model M. An estimator
b
θ
n
is UANU in model M if there exists sequences σ
n
(P ) such that the z-statistic
b
θ
n
− θ (P )
/σ
n
(P ) converges uniformly to a standard normal random variable in the following sense: for t ∈ R,
sup
P ∈M
|Pr
P
h
n
1/2
b
θ
n
− θ (P )
/σ
n
(P ) < t
i
− Φ (t) | → 0 as n → ∞
where Φ (t) is the standard normal cumulative distribution function (Robins and Ritov,1997).
All inconsistent estimators and some consistent estimators (see Chapter 18 for examples) are biased under this
definition. In this book, when we say an estimator is unbiased (without further qualification) we mean that it is UANU.
or A = 0. Because of the presence of random sampling variability, we do
not expect that exchangeability will exactly hold in our sample. For example,
suppose that only the 20 individuals in our study were randomly assigned to
either heart transplant (A = 1) or medical treatment (A = 0). Suppose further
that each individual can be classified as good or bad prognosis at the time of
randomization. We say that the groups A = 0 and A = 1 are exchangeable
if they include exactly the same proportion of individuals with bad prognosis.
By chance, it is possible that 2 out of the 13 individuals assigned to A = 1
and 3 of the 7 individuals assigned to A = 0 had bad prognosis. However, if
we increased the size of our sample then there is a high probability that the
relative imbalance between the groups A = 1 and A = 0 would decrease.
Under this conceptualization, there are two possible targets for inference.
First, investigators may be agnostic about the existence of a super-population
and restrict their inference to the sample that was actually randomized. This is
referred to as randomization-based inference, and requires taking into accountSee Robins (1988) and Green-
land (1991) for a discussion of
randomization-based inference.
some technicalities that are beyond the scope of this book. Second, investiga-
tors may still be interested in making inferences about the super-population
from which the study sample was randomly drawn. From an inference stand-
136 Random variability
Fine Point 10.2
Uncertainty from systematic biases. The width of the usual Wald-type confidence intervals is a function of the
standard error of the estimator and thus reflects only uncertainty due to random error. However, the possible presence
of systematic bias due to confounding, selection, or measurement is another important source of uncertainty. The larger
the study population, the smaller the random error is both absolutely and as a proportion of total uncertainty, and hence
the more the usual Wald confidence interval will understate the true uncertainty.
The stated 95% confidence in a 95% confidence interval becomes overconfidence as population size increases because
the interval excludes uncertainty due to systematic biases, which are not diminished by increasing the sample size. As
a consequence, some authors advocate referring to such intervals by a less confident name, calling them compatibility
intervals instead. The renaming recognizes that such intervals can only show us which effect sizes are highly compatible
with the data under our adjustment assumptions and methods (Amrhein et al. 2019; Greenland 2019). The compatibility
concept is weaker than the confidence concept, for it does not demand complete confidence that our adjustment removes
all systematic biases.
Regardless of the name of the intervals, the uncertainty due to systematic bias is usually a central part of the discussion
section of scientific articles. However, most discussions revolve around informal judgments about the potential direction
and magnitude of the systematic bias. Some authors argue that quantitative methods need to be used to produce
intervals around the effect estimate that integrate random and systematic sources of uncertainty. These methods are
referred to as quantitative bias analysis. See the book by Lash, Fox, and Fink (2009). Bayesian alternatives are discussed
by Greenland and Lash (2008), and Greenland (2009a, 2009b).
point, this latter case turns out to be mathematically equivalent to the con-
ceptualization of sampling variability described at the start of this section in
which the entire super-population was randomly assigned to treatment. That
is, randomization followed by random sampling is equivalent to random sam-
pling followed by randomization.
In many cases we are not interested in the first target. To see why, consider
a study that compares the effect of two first-line treatments on the mortality
of cancer patients. After the study ends, we may determine that it is better
to initiate one of the two treatments, but this information is now irrelevant
to the actual study participants. The purpose of the study was not to guide
the choice of treatment for patients in the study but rather for a group of
individuals similar to—but larger than—the studied sample. Heretofore we
have assumed that there is a larger group—the super-population—from which
the study participants were randomly sampled. We now turn our attention to
the concept of the super-population.
10.3 The myth of the super-population
As discussed in Chapter 1, there are two sources of randomness: sampling
variability and nondeterministic counterfactuals. Below we discuss both.
Consider our estimate
c
Pr[Y = 1 | A = 1] = ˆp = 7/13 of the super-
population risk Pr[Y = 1|A = a] = p. Nearly all investigators would report a
binomial confidence interval ˆp±1.96
q
ˆp(1−ˆp)
n
= 7/13±1.96
q
(7/13)(6/13)
13
for the
probability p. If asked why these intervals, they would say it is to incorporate
the uncertainty due to random variability. But these intervals are valid only
if ˆp has a binomial sampling distribution. So we must ask when would that
happen. In fact there are two scenarios under which ˆp has a binomial sampling
10.3 The myth of the super-population 137
distribution.
• Scenario 1. The study population is sampled at random from an es-
sentially infinite super-population, sometimes referred to as the source
or target population, and our estimand is the proportion p = Pr[Y =The term i.i.d. used in Techni-
cal Point 10.1 means that our data
were a random sample of size n
from a super-population.
1|A = 1] of treated individuals who developed the outcome in the super-
population. It is then mathematically true that, in repeated random
samples of size 13 from the treated individuals in the super-population,
the number of individuals who develop the outcome among the 13 is a
binomial random variable with success probability Pr[Y = 1|A = 1]. As
a result, the 95% Wald confidence interval calculated in the previous sec-
tion is asymptotically calibrated for Pr[Y = 1|A = 1]. This is the model
we have considered so far.Robins (1988) discussed these two
scenarios in more detail.
• Scenario 2. The study population is not sampled from a hypothetical
super-population. Rather (i) each individual i among the 13 treated in-
dividuals has an individual nondeterministic (stochastic) counterfactual
probability p
a=1
i
(ii) the observed outcome Y
i
= Y
a=1
i
for subject i oc-
curs with probability p
a=1
i
and (iii) p
a=1
i
takes the same value, say p, for
each of the 13 treated individuals. Then the number of individuals who
develop the outcome among the 13 treated is a binomial random vari-
able with success probability p. As a result, the 95% confidence interval
calculated in the previous section is asymptotically calibrated for p.
Scenario 1 assumes a hypothetical super-population. Scenario 2 does not.
However, Scenario 2 is untenable because the probability p
a=1
i
of developing
the outcome when treated will almost certainly vary among the 13 treated in-
dividuals due to between-individual differences in risk. For example we would
expect the probability of death p
a=1
i
to have some dependence on an indi-
vidual’s genetic make-up. If the p
a=1
i
are nonconstant then the estimand of
interest in the actual study population would generally be the average, say p, of
the 13 p
a=1
i
. But in that case the number of treated who develop the outcome
is not a binomial random variable with success probability p, and the 95% con-
fidence interval for p calculated in the previous section is not asymptotically
calibrated but conservative.
Therefore, any investigator who reports a binomial confidence interval for
Pr[Y = 1|A = a], and who acknowledges that there exists between-individual
variation in risk, must be implicitly assuming Scenario 1: the study individuals
were sampled from a near-infinite super-population and that all inferences are
concerned with quantities from that super-population. Under Scenario 1, the
number with the outcome among the 13 treated is a binomial variable regard-
less of whether the underlying counterfactual is deterministic or stochastic.
An advantage of working under the hypothetical super-population scenario
is that nothing hinges on whether the world is deterministic or nondetermin-
istic. On the other hand, the super-population is generally a fiction; in most
studies individuals are not randomly sampled from any near-infinite popula-
tion. Why then has the myth of the super-population endured? One reason is
that it leads to simple statistical methods.
A second reason has to do with generalization. As we mentioned in the
previous section, investigators generally wish to generalize their findings about
treatment effects from the study population (e.g., the 20 individuals in our
heart transplant study) to some large target population (e.g., all immortals in
the Greek pantheon). The simplest way of doing so is to assume the study
population is a random sample from a large population of individuals who
138 Random variability
are potential recipients of treatment. Since this is a fiction, a 95% confi-
dence interval computed under Scenario 1 should be interpreted as covering
the super-population parameter had, often contrary to fact, the study individ-
uals been sampled randomly from a near infinite super-population. In other
words, confidence intervals obtained under Scenario 1 should be viewed as
what-if statements.
It follows from the above that an investigator might not want to entertain
Scenario 1 if the size of the pool of potential recipients is not much larger
than the size of the study population, or if the target population of potential
recipients is believed to differ from the study population to an extent that
cannot be accounted for by sampling variability. Here we will accept that
individuals were randomly sampled from a super-population, and explore the
consequences of random variability for causal inference in that context. We
first explore this question in a simple randomized experiment.
10.4 The conditionality “principle”
Table 10.1 summarizes the data from a randomized trial to estimate the average
causal effect of treatment A (1: yes, 0: no) on the 1-year risk of death Y (1:
yes, 0: no). The experiment included 240 individuals, 120 in each treatment
group. The associational risk difference is Pr[Y = 1|A = 1] − Pr[Y = 1|A =
0] =
24
120
−
42
120
= −0.15. Suppose the experiment had been conducted in a
super-population of near-infinite size, the treated and the untreated would be
exchangeable, i.e., Y
a
⊥⊥A, and the associational risk difference would equal
the causal risk difference Pr
Y
a=1
= 1
− Pr
Y
a=0
= 1
. Suppose the studyThe estimated variance of the un-
adjusted estimator is
24
120
96
120
120
+
42
120
78
120
120
=
31
9600
. The Wald
95% confidence interval is then
−0.15 ±
31
9600
1/2
× 1.96 =
(−0.26, −0.04).
investigators computed a 95% confidence interval (−0.26, −0.04) around the
point estimate −0.15 and published an article in which they concluded that
treatment was beneficial because it reduced the risk of death by 15 percentage
points.
However, the study population had only 240 individuals and is therefore
likely that, due to chance, the treated and the untreated are not perfectly
exchangeable. Random assignment of treatment does not guarantee exact ex-
changeability for the sample consisting of the 240 individuals in the trial; it onlyTable 10.1
Y = 1 Y = 0
A = 1 24 96
A = 0 42 78
guarantees that any departures from exchangeability are due to random vari-
ability rather than to a systematic bias. In fact, one can view the uncertainty
resulting from our ignorance of the chance correlation between unmeasured
baseline risk factors and the treatment A in the study sample as contributing
to the length 0.22 of the confidence interval.
A few months later the investigators learn that information on a third
variable, cigarette smoking L (1: yes, 0: no), had also been collected and decideTable 10.2
L = 1 Y = 1 Y = 0
A = 1 4 76
A = 0 2 38
L = 0 Y = 1 Y = 0
A = 1 20 20
A = 0 40 40
to take a look at it. The study data, stratified by L, is shown in Table 10.2.
Unexpectedly, the investigators find that the proportion of individuals receiving
treatment among smokers (80/120) is twice that among nonsmokers (40/120),
which suggests that the treated and the untreated are not exchangeable and
thus that adjustment for smoking is necessary. When the investigators adjust
via stratification, the associational risk difference in smokers, Pr[Y = 1|A =
1, L = 1] − Pr[Y = 1|A = 0, L = 1], is equal to 0. The associational risk
difference in nonsmokers, Pr[Y = 1|A = 1, L = 0] − Pr[Y = 1|A = 0, L = 0],
is also equal to 0. The adjusted analysis suggests treatment has no effect in
both smokers and nonsmokers, even though the marginal risk difference −0.15
suggested a net beneficial effect in the study population.
10.4 The conditionality “principle” 139
Technical Point 10.2
A formal statement of the conditionality principle. The likelihood for the observed data has three factors: the
density of Y given A and L, the density of A given L, and the marginal density of L. Consider a simple example with
one dichotomous L, exchangeability Y
a
⊥⊥A|L, the stratum-specific risk difference sRD = Pr (Y = 1|L = l, A = 1) −
Pr (Y = 1|L = l, A = 0) known to be constant across strata of L, and in which the parameter of interest is the stratum-
specific causal risk difference. Then the likelihood of the data is
n
Y
i=1
f (Y
i
|L
i
, A
i
; sRD, p
0
) × f (A
i
|L
i
; α) × f (L
i
; ρ)
where p
0
= (p
01
, p
02
) with p
0l
= Pr (Y = 1|L = l, A = 0), α, and ρ are nuisance parameters associated with the
conditional density of Y given A and L, the conditional density of A given L, and the marginal density of L, respectively.
See, for example, Casella and Berger (2002).
The data on A and L are said to be S-ancillary for the parameter of interest when, as in this case, the distribution
of the data conditional on these variables depends on the parameter of interest, but the joint density of A and L does
not share parameters with f (Y
i
|L
i
, A
i
; sRD, p
0
). The conditionality principle states that one should always perform
inference on the parameter of interest conditional on any S-ancillary statistics. Thus one should condition on the S-
ancillary statistic {A
i
, L
i
; i = 1, .., n}. Analogously, if the risk ratio (rather than the risk difference) were known to be
constant across strata of L, {A
i
, L
i
; i = 1, .., n} remains S-ancillary for the risk ratio.
An exact ancillary statistic is defined to be an S-ancillary statistic whose marginal distribution is known. In our
example, this would require that α and ρ be known.
These new findings are disturbing to the investigators. Either someone didThe estimated variance of the ad-
justed estimator is described in
Technical Point 10.5. The Wald
95% confidence interval is then
(−0.076, 0.076).
not assign the treatment at random (malfeasance) or randomization did not
result in approximate exchangeability (very very bad luck). A debate ensues
among the investigators. Should they retract their article and correct the
results? They all agree that the answer to this question would be affirmative
if the problem were due to malfeasance. If that were the case, there would
be confounding by smoking and the effect estimate should be adjusted for
smoking. But they all agree that malfeasance is impossible given the study’s
quality assurance procedures. It is therefore clear that the association between
smoking and treatment is entirely due to bad luck. Should they still retract
their article and correct the results?
One investigator says that they should not retract the article. His argument
goes as follows: “Okay, randomization went wrong for smoking, but why should
we privilege the adjusted over the unadjusted estimator? It is likely that
imbalances on other unmeasured factors U cancelled out the effect of the chance
imbalance on L, so that the unadjusted estimator is still the closer to the true
value in the super-population.” A second investigator says that they should
retract the article and report the adjusted null result. Her argument goes as
follows: “We should adjust for L because the strong association between L and
A introduces confounding in our effect estimate. Within levels of L, we have
mini randomized trials and the confidence intervals around the corresponding
point estimates will reflect the uncertainty due to the possible U-A associations
conditional on L.”
To determine which investigator is correct, here are the facts of the matter.
Suppose, for simplicity, the true causal risk difference is constant across strata
of L, and suppose we could run the randomized experiment trillions of times.
We then select only (i.e., condition on) those runs in which smoking L and
140 Random variability
Technical Point 10.3
Approximate ancillarity. Suppose that the stratum-specific risk difference (sRD
l
) is known to vary over strata of L.
Under our usual identifiability assumptions, the causal risk difference in the population is identified by the standardized
risk difference
RD
std
=
X
l
[Pr (Y = 1|L = l, A = 1; υ) − Pr (Y = 1|L = l, A = 0; υ)] f (l; ρ)
which depends on the parameters υ = {sRD
l
, p
0,l
; l = 0, 1} and ρ (see Technical Point 10.2). In unconditionally
randomized experiments, RD
std
equals the associational RD, Pr (Y = 1|A = 1) − Pr (Y = 1|A = 0), because A⊥⊥L
in the super-population. Due to the dependence of RD
std
on ρ, {A
i
, L
i
; i = 1, .., n} is no longer exactly ancillary and
in fact no exact ancillary exists.
Consider the statistic
e
S =
d
OR
AL
− OR
AL
where OR
AL
= OR
AL
(α) =
Pr(A=1|L=1;α) Pr(A=0|L=0;α)
Pr(A=1|L=0;α) Pr(A=0|L=1;α)
is the A-L
odds ratio in the super-population, and
d
OR
AL
is OR
AL
but with the the population proportions Pr (A = a|L = l; α)
replaced by the empirical sample proportions
c
Pr (A = a|L = l).
e
S is asymptotically normal with mean 0 conditional on
the L
i
and thus its distribution depends on α. Let
b
S =
e
S/ bse(
e
S), where bse(
e
S) is an estimate of the standard error of
e
S. The distribution of
b
S converges to a standard normal distribution in large samples, so that
b
S quantifies the A-L
association in the data on a standardized scale. For example, if
b
S = 2, then
b
S is two standard deviations above its
(asymptotic) expected value of 0.
When the true value of OR
AL
is known,
b
S is referred to as an approximate (or large sample) ancillary statistic. To see
why, consider a randomized experiment with OR
AL
= 1. Then
b
S, like an exact ancillary statistic, i) can be computed
from the data (i.e.,
b
S =
d
OR
AL
− 1
/ bse(
e
S)), ii)
b
S has an approximately known distribution, iii) the likelihood factors
into a term f (A|L; α) that governs the distribution of
e
S and a term f (Y |L, A; υ) f (L; ρ) that does not depend on α,
and iv) conditional on
b
S, the adjusted estimate of RD
std
is unbiased, while the unadjusted estimate of RD
std
is biased
(Technical Point 10.4 defines and compares adjusted and unadjusted estimators). Any other statistic that quantifies the
A-L association
c
Pr(A=1|L=1)
c
Pr(A=1|L=0)
− 1, can be used in place of
e
S.
Now consider a continuity principle wherein inferences about an estimand should not change discontinuously in
response to an arbitrarily small known change in the data generating distribution (Buehler 1982). If one accepts both
the conditionality and continuity principles, then one should condition on an approximate ancillary statistic. For example,
when OR
AL
= 1 is known, the continuity principle would be violated if, following the conditionality principle, we treated
the unadjusted estimate of RD
std
as biased when sRD
l
was known to be a constant, but treated it as unbiased when
the sRD
l
were almost constant. We will say that a researcher who always conditions on both exact and approximate
ancillaries follows the extended conditionality principle.
treatment A are as strongly positively associated as in the observed data. We
would find that, within each level of L, the fraction of these runs in which
any given pre-treatment risk factor U for Y was positively associated with
A essentially equals the number of runs in which it was negatively associated.
(This is true even if U and L are highly correlated in both the super-population
and in the study data.)
As a consequence, the adjusted estimate of the treatment effect is unbiased
but the unadjusted estimate is greatly biased when averaged over these runs.
Unconditionally—over all the runs of the experiment—both the unadjustedThe unconditional efficiency of the
adjusted estimator results from the
adjusted estimator being the maxi-
mum likelihood estimator (MLE) of
the risk difference when data on L
are available.
and adjusted estimates are unbiased but the variance of the adjusted estimate
is smaller than that of the unadjusted estimate. That is, the adjusted estimator
is both conditionally unbiased and unconditionally more efficient. Hence either
from the conditional or unconditional point of view, the Wald interval centered
on the adjusted estimator is the better analysis and the article needs to be
retracted. The second investigator is correct.
10.4 The conditionality “principle” 141
Technical Point 10.4
Comparison between adjusted and unadjusted estimators. The adjusted estimator of RD
std
in Technical Point
10.3 is the parametric maximum likelihood estimator
d
RD
MLE
, which replaces the population proportions in the RD
std
by their sample proportions. The unadjusted estimator of RD
std
is
d
RD
UN
=
c
Pr (Y = 1|A = 1) −
c
Pr (Y = 1|A = 0).
Unconditionally, both
d
RD
MLE
and
d
RD
UN
are asymptotically normal and unbiased for RD
std
with asymptotic variances
aV ar
d
RD
MLE
and aV ar
d
RD
UN
.
In the text we stated that
d
RD
UN
is both unconditionally inefficient and conditionally biased. We now explain that
both properties are logically equivalent. Robins and Morgenstern (1987) prove that
d
RD
MLE
has the same asymptotic
distribution conditional on the approximate ancillary
b
S as it does unconditionally, which implies aV ar
d
RD
MLE
=
aV ar
d
RD
MLE
|
b
S
. They also show that aV ar
d
RD
MLE
equals aV ar
d
RD
UN
−
h
aCov
b
S,
d
RD
UN
i
2
. Hence
d
RD
UN
is unconditionally inefficient if and only if aCov
b
S,
d
RD
UN
= 0, i.e.,
b
S and
d
RD
UN
are correlated uncondition-
ally. Further, the conditional asymptotic bias a E
h
d
RD
UN
|
b
S
i
− RD
std
is shown to equal aCov
b
S,
d
RD
UN
b
S. Hence,
d
RD
UN
is conditionally biased if and only if it is unconditionally inefficient.
It can be shown that aCov
b
S,
d
RD
UN
= 0 if and only if L⊥⊥Y |A. Therefore, when data on a measured risk factor
for Y are available,
d
RD
MLE
is preferred over
d
RD
UN
. The estimator
d
RD
UN
− aCov
b
S,
d
RD
UN
b
S corrects the bias
of
d
RD
UN
, and thus has the same asymptotic distribution as
d
RD
MLE
given the approximate ancillary
b
S.
The idea that one should condition on the observed L-A association is an
example of what is referred to in the statistical literature as the conditionality
principle. In statistics, the observed L-A association is said to be an ancillary
statistic for the causal risk difference. The conditionality principle states that
inference on a parameter should be performed conditional on ancillary statistics
(see Technical Points 10.2 and 10.3 for details).
In the above discussion about the findings of the randomized experiment,
some of the investigators intuitively followed the conditionality principle be-
cause they considered an estimator to be biased when it cannot center a valid
Wald confidence interval conditional on any ancillary statistics. For such re-
searchers, our previous definition of bias was not sufficiently restrictive. They
would say that an estimator is unbiased if and only if it can center a valid
Wald interval conditional on ancillary statistics. Technical Point 10.5 argues
that most researchers implicitly follow the conditionality principle.
When confronted with the frequentist argument that “Adjustment for L
is unnecessary because unconditionally—over all the runs of the experiment—
the unadjusted estimate is unbiased,” investigators that intuitively apply the
conditionality principle would aptly respond “Why should the various L-A
associations in other hypothetical studies affect what I do in my study? In my
study L acts as a confounder and adjustment is needed to eliminate bias.” This
is a convincing argument for both randomized experiments and observational
studies as long as, like in the randomized experiment of our example, the
number of measured confounders is not large. However, when the number of
measured confounders is large, strictly following the conditionality principle is
no longer a wise strategy.
142 Random variability
Technical Point 10.5
Most researchers intuitively follow the extended conditionality principle. Consider again the randomized trial data
in Table 10.2. Assuming without loss of generality that the sRD is constant over the strata of a dichotomous L, the
estimated variance of the MLE of sRD is
b
V
0
b
V
1
/
b
V
0
+
b
V
1
where
b
V
l
is the estimated variance of
d
RD
l
.
Two possible choices for
b
V
1
are
b
V
obs
1
=
4
80
76
80
80
+
2
40
38
40
40
= 1.78 ×10
−3
= and
b
V
exp
1
=
4
80
76
80
60
+
2
40
38
40
60
= 1.58 ×10
−3
that
differ only in that
b
V
obs
1
divides by the observed number of individuals in stratum L = 1 with A = 1 and A = 0 (80 and
40, respectively) while
b
V
exp
1
divides by the expected number of subjects (60) given that A⊥⊥L. Mathematically,
b
V
obs
1
is
the variance estimator based on the observed information and
b
V
exp
1
is the estimator based on the expected information.
In our experience, nearly all researchers would choose
b
V
obs
1
over
b
V
exp
1
as the appropriate variance estimator. Results of
Efron and Hinkley (1978) and Robins and Morgenstern (1987) imply that such researchers are implicitly conditioning on
an approximate ancillary
b
S and thus, whether aware of this fact or not, are following the extended conditionality principle.
Specifically, these authors proved that the variance of
d
RD
l
, and thus of the MLE, conditioned on an approximate
ancillary
b
S differs from the unconditional variance by order n
−3/2
. (As noted in Technical Point 10.4, the conditional
and unconditional asymptotic variance of an MLE are equal, as equality of asymptotic variances implies equality only
up to order n
−1
.) Further, they showed that the variance estimator based on the observed information differs from the
conditional variance by less than order n
−3/2
, while an estimator based on the expected information differs from the
unconditional variance by less than n
−3/2
. Thus, a preference for
b
V
obs
1
over
b
V
exp
1
implies a preference for conditional
over unconditional inference.
10.5 The curse of dimensionality
The derivations in previous sections above are based on an asymptotic theory
that assumed the number of strata of L was small compared with the sample
size. In this section, we study the cases in which the number of strata of a
vector L can be very large, even much larger than the sample size.
Suppose the investigators had measured 100 pre-treatment binary variables
rather than only one, then the pre-treatment variable L formed by combining
the 100 variables L = (L
1
, ..., L
100
) has 2
100
strata. When, as in this case,
there are many possible combinations of values of the pre-treatment variables,
we say that the data is of high dimensionality. For simplicity, suppose that
there is no additive effect modification by L, i.e., the super-population risk
difference Pr[Y = 1|A = 1, L = l] − Pr[Y = 1|A = 0, L = l] is constant across
the 2
100
strata. In particular, suppose that the constant stratum-specific risk
difference is 0.
The investigators debate again whether to retract the article and report
their estimate of the stratified risk difference. They have by now agreed that
they should follow the conditionality principle because the unadjusted risk
difference −0.15 is conditionally biased. However, they notice that, when there
are 2
100
strata, a 95% confidence interval for the risk difference based on the
adjusted estimator is much wider than that based on the unadjusted estimator.
This is exactly the opposite of what was found when L had only two strata.
In fact, the 95% confidence interval based on the adjusted estimator may be
so wide as to be completely uninformative.
To see why, note that, because 2
100
is much larger than the number of
individuals (240), there will at most be only a few strata of L that will contain
both a treated and an untreated individual. Suppose only one of 2
100
strata
contains a single treated individual and a single untreated individual, and no
other stratum contains both a treated and untreated individual. Then the
10.5 The curse of dimensionality 143
Technical Point 10.6
Can the curse of dimensionality be reversed? In high-dimensional settings with many strata of L, informative
conditional inference for the common risk difference given the exact ancillary statistic {A
i
, L
i
; i = 1, ..n} is not possible
regardless of the estimator used. This is not true for unconditional inference in marginally randomized experiments. For
example, the unconditional statistical behavior of the unadjusted estimator
d
RD
UN
is unaffected by the dimension of
L. In particular, it remains unbiased with the width of the associated Wald 95% confidence interval proportional to
1/n
1/2
. Because
d
RD
UN
relies on prior information not used by the MLE, it is an unbiased estimator of the common
risk difference only if it is known that A⊥⊥L in the super-population.
However, even unconditionally, the confidence intervals associated with the MLE, i.e., the adjusted estimator, remain
uninformative. This raises the question of whether data on L can be used to construct an estimator that is also
unconditionally unbiased but that is more efficient that the unadjusted estimator. In Chapter 18 we show that this is
sometimes possible.
95% confidence interval for the common risk difference based on the adjusted
estimator is (−1, 1) , and therefore completely uninformative, because in the
single stratum with both a treated and an untreated individual, the empirical
risk difference could be −1, 0, or 1 depending on the value of Y for each indi-
vidual. In contrast, the 95% confidence interval for the common risk difference
based on the unadjusted estimator remains (−0.26, −0.04) as above because
its width is unaffected by the fact that more covariates were measured. These
results reflect the fact that the adjusted estimator is only guaranteed to be
more efficient than the unadjusted estimator when the ratio of number of indi-
viduals to the number of unknown parameters is large (a frequently used rule
of thumb is a minimum ratio of 10, though the minimum ratio depends on the
characteristics of the data).
What should the investigators do? By trying to do the right thing—
following the conditionality principle—in the simple setting with one dichoto-
mous variable, they put themselves in a corner for the high-dimensional set-
ting. This is the curse of dimensionality: conditional on all 100 covariates
the marginal estimator is still biased, but now the conditional estimator is
uninformative. This shows that, just because conditionality is compelling inRobins and Ritov (1997) provide a
technical description of the curse of
dimensionality.
simple examples, it should not be raised to a principle since it cannot be car-
ried through for high-dimensional models. Though we have discussed this issue
in the context of a randomized experiment, our discussion applies equally to
observational studies. See Technical Point 10.6.
Finding a solution to the curse of dimensionality is a difficult problem and
an active area of research. In Chapter 18 we review this research and offer some
practical guidance. Chapters 11 through 17 provide necessary background
information on the use of models for causal inference.
144 Random variability
Technical Point 10.7
Implications of random variability for causal discovery. In Fine Point 6.3 we explained that, under faithfulness, we
could sometimes learn the causal structure if we had an infinite amount of data. After the concepts introduced in this
chapter, we are now ready to consider the implications for causal discovery of only having a finite sample.
Suppose we have data on 3 variables Z, A, Y and we know that their time sequence is Z first, A second, and Y last.
Our data analysis finds that the empirical odds ratio of Y and Z equal to 1 at every level of A. All other odds ratios,
marginal and conditional, are far from 1. In Fine Point 6.3 we showed that, if Z⊥⊥Y |A in the super-population (which
would require an infinite sample size) then, under faithfulness, the only possible causal diagram is Z → A → Y with
perhaps a common cause U of Z and A in addition to (or in place of) the arrow from Z to A. It follows that the risk
difference E[Y |A = 1] − E[Y |A = 0] is the average causal effect of A on Y . But, in practice, evidence of conditional
or unconditional independence must be based on a finite sample size.
Robins et al. (2003) showed that, even if one is willing to assume faithfulness, inferences based on faithfulness are
non-uniform, i.e., no matter how big the sample size n, even if the empirical odds ratio of Y and Z were equal to 1
at every level of A, there exist faithful distributions with the following properties: a) due to sampling variability, the
true odds ratio of Y and Z at each level of A, although not equal to 1, is so close to 1 that empirical conditional
odds ratios of 1 are unsurprising, and yet b) the average causal effect of A on Y is zero. As a consequence, no honest
95% frequentist confidence interval for the average causal effect of A on Y can ever exclude the value 0 even when
the empirical risk difference estimate of E[Y |A = 1] − E[Y |A = 0] is quite large (say, 0.2) and is many (say 30) times
greater than its standard error.
Even so, advocates of causal discovery may cogently argue that, given the empirical data above, a Bayesian (with
priors not depending on sample size) who believes in faithfulness will generally have a (highest posterior density) 95%
credible interval for the average causal effect of A on Y that is nearly centered on the empirical risk difference, with
width not much greater than the standard error of the empirical risk difference. Thus, this credible interval easily
excludes zero whenever graphs with Z and Y d-separated by A are given a non-negligible prior probability.
The striking difference between the honest frequentist confidence intervals and these credible intervals is a consequence
of the fact that Bayesian inference for causal effects can be very sensitive to choice of prior in the causal discovery
setting. For example, many epidemiologists, including the authors, would argue that, in an observational study, the
prior probability given to any causal diagram that lacks a common cause of A and Y (such as the graph Z → A → Y )
should be essentially zero. To believe otherwise, A and Y must have had no common cause from the big bang till now.
A Bayesian who shares our prior belief may have (depending on other aspects of the prior) a 95% credible interval much
wider and with a center much closer to 0 than the credible interval described above.
In summary, in finite samples and even under faithfulness, data alone cannot distinguish the causal diagram Z → A →
Y under which Z⊥⊥Y |A in the super-population from another causal diagram under which Z is almost independent of
Y given A in the super-population. Therefore the validity of causal discovery from observational data relies heavily on
a priori subject-matter knowledge about the plausibility of various causal diagrams.
Part II
Causal infe rence with models
Chapter 11
WHY MODEL?
Do not worry. No more chapter introductions around the effect of your looking up on other people’s looking up.
We squeezed that example well beyond what seemed possible. In Part II of this book, most examples involve real
data. The data sets can be downloaded from the book’s web site.
Part I was mostly conceptual. Calculations were kept to a minimum, and could be carried out by hand. In
contrast, the material described in Part II requires the use of computers to fit regression models, such as linear
and logistic models. Because this book cannot provide a detailed introduction to regression techniques, we assume
that readers have a basic understanding and working knowledge of these commonly used models. Our web site
provides links to computer code in R, SAS, Stata, and Python to replicate the analyses described in the text. The
code margin notes specify the portion of the code that is relevant to the analysis described in the text.
This chapter describes the differences between the nonparametric estimators used in Part I and the parametric
(model-based) estimators used in Part II. It also reviews the concept of smoothing and, briefly, the bias-variance
trade-off involved in any modeling decision. The chapter motivates the need for models in data analysis, regardless
of whether the analytic goal is causal inference or, say, prediction. We will take a break from causal considerations
until the next chapter. Please bear in mind that the statistical literature on modeling is vast; this chapter can
only highlight some of the key issues.
11.1 Data cannot speak for themselves
Consider a study population of 16 individuals infected with the human im-
munodeficiency virus (HIV). Unlike in Part I of this book, we will not view
these individuals as representatives of 1 billion individuals identical to them.
Rather, these are just 16 individuals randomly sampled from a large, possibly
hypothetical super-population: the target population.
At the start of the study each individual receives a certain level of a treat-
ment A (antiretroviral therapy), which is maintained during the study. At the
end of the study, a continuous outcome Y (CD4 cell count, in cells/mm
3
) is
measured in all individuals. We wish to consistently estimate the mean of Y
among individuals with treatment level A = a in the population from which the
16 individuals were randomly sampled. That is, the estimand is the unknown
population parameter E[Y |A = a].
As defined in Chapter 10, an estimator
b
E[Y |A = a] of E[Y |A = a] is some
function of the data that is used to estimate the unknown population parame-
ter. Informally, a consistent estimator
b
E[Y |A = a] meets the requirement thatSee Chapter 10 for a rigorous defi-
nition of a consistent estimator. “the larger the sample size, the closer the estimate to the population value
E[Y |A = a].” Two examples of possible estimators
b
E[Y |A = a] are (i) the
sample average of Y among those receiving A = a, and (ii) the value of the
first observation in the dataset that happens to have the value A = a. The
sample average of Y among those receiving A = a is a consistent estimator of
the population mean; the value of the first observation with A = a is not. In
practice we require all estimators to be consistent, and therefore we use the
sample average to estimate the population mean.
148 Why model?
Suppose treatment A is a dichotomous variable with two possible values: no
treatment (A = 0) and treatment (A = 1). Half of the individuals were treated
(A = 1). Figure 11.1 is a scatter plot that displays each of the 16 individuals
as a dot. The height of the dot indicates the value of the individual’s outcome
Figure 11.1
Y . The 8 treated individuals are placed along the column A = 1, and the 8
untreated along the column A = 0. As defined in Chapter 10, an estimate of
the mean of Y among individuals with level A = a in the population is the
numerical result of applying the estimator—in our case, the sample average—to
a particular data set.
Our estimate of the population mean in the treated is the sample aver-
age 146.25 for those with A = 1, and our estimate of the population mean
in the untreated is the sample average 67.50 in those with A = 0. Under ex-
changeability of the treated and the untreated, the difference 146.25 − 67.50
would be interpreted as an estimate of the average causal effect of treatment
A on the outcome Y in the target population. However, this chapter is not
about making causal inferences. Our current goal is simply to motivate the
need for models when trying to estimate population quantities like the mean
E[Y |A = a], irrespective of whether the estimates do or do not have a causal
interpretation.
Now suppose treatment A is a polytomous variable that can take 4 possible
values: no treatment (A = 1), low-dose treatment (A = 2), medium-dose treat-
ment (A = 3), and high-dose treatment (A = 4). A quarter of the individuals
received each treatment level. Figure 11.2 displays the outcome value for the
16 individuals in the study population. To estimate the population means in
the 4 groups defined by treatment level, we compute the corresponding sample
averages. The estimates are 70.0, 80.0, 117.5, and 195.0 for A = 1, A = 2,code: Program 11.1
A = 3, and A = 4, respectively.
Figure 11.2
Figures 11.1 and 11.2 depict examples of discrete (categorical) variables
with 2 and 4 categories, respectively. Because the number of study individuals
is fixed at 16, the number of individuals per category decreases as the number
of categories increases. The sample average in each category is still an exactly
unbiased estimator of the corresponding population mean, but the probability
that the sample average is close to the corresponding population mean de-
creases as the number of individuals in each category decreases. The length of
the 95% confidence intervals (see Chapter 10) for the category-specific means
will be greater for the data in Figure 11.2 than for the data in Figure 11.1.
Finally, suppose that A represents the dose of treatment in mg/day, and
that it takes integer values from 0 to 100 mg. Figure 11.3 displays the outcome
Figure 11.3
value for each of the 16 individuals. Because the number of possible values of
treatment is much greater than the number of individuals in the study, there
are many values of A that no individual received. For example, there are no
individuals with treatment dose A = 90 in the study population.
This creates a problem: how can we estimate the mean of the outcome Y
among individuals with treatment level A = 90 in the target population? The
estimator we used for the data in Figures 11.1 and 11.2—the treatment-specific
sample average—is undefined for treatment levels for which there are zero in-
dividuals in Figure 11.3. If treatment A were a truly continuous variable, then
the sample average would be undefined for nearly all treatment levels. (A con-
tinuous variable A can be viewed as a categorical variable with an uncountably
infinite number of categories.)
The above description shows that we cannot always let the data “speak
for themselves” to obtain a meaningful estimate. Rather, we often need to
supplement the data with a model, as we describe in the next section.
11.2 Parametric estimators of the conditional mean 149
11.2 Parametric estimators of the conditional mean
We want to estimate the mean of Y among individuals with treatment level
A = 90, i.e., E[Y |A = 90], from the data in Figure 11.3. Suppose we expect the
mean of Y among individuals with treatment level A = 90 to lie between the
mean among individuals with A = 80 and the mean among individuals with
A = 100. In fact, suppose we knew that the treatment-specific population
mean of Y is a linear function of the value of treatment A throughout the
range of A. More precisely, we know that the mean of Y , E[Y |A], increases (or
decreases) from some value θ
0
for A = 0 by θ
1
units per unit of A. Or, more
compactly,
E[Y |A] = θ
0
+ θ
1
A
This equation is a restriction on the shape of conditional mean function E[Y |A].More generally, the restriction on
the shape of the relation is known
as the functional form and, by
some authors, as the dose-response
curve. We do not use the latter
term because it suggests that the
dose of treatment causally effects
the response, which could be false
in the presence of confounding.
This particular restriction is referred to as a linear mean model, and the quan-
tities θ
0
and θ
1
are referred to as the parameters of the model. Models that
describe the conditional mean function in terms of a finite number of param-
eters are referred to as parametric conditional mean models. In our example,
the parameters θ
0
and θ
1
define a straight line that crosses (intercepts) the
vertical axis at θ
0
and that has a slope θ
1
. That is, the model specifies that
all conditional mean functions are straight lines, though their intercepts and
slopes may vary.
We are now ready to combine the data in Figure 11.3 with our parametric
mean model to estimate E[Y |A = a] for all values a from 0 to 100. The first
step is to obtain estimates
ˆ
θ
0
and
ˆ
θ
1
of the parameters θ
0
and θ
1
. The second
step is to use these estimates to estimate the mean of Y for any value A = a.
Figure 11.4
For example, to estimate the mean of Y among individuals with treatment
level A = 90, we use the expression
b
E[Y |A = 90] =
ˆ
θ
0
+ 90
ˆ
θ
1
. The estimate
b
E[Y |A] for each individual is referred to as the predicted value.
An exactly unbiased estimator of θ
0
and θ
1
can be obtained by the method
of ordinary least squares. A nontechnical motivation of the method follows.
Consider all possible candidate straight lines for Figure 11.3, each of them
with a different combination of values of intercept θ
0
and slope θ
1
. For each
candidate line, one can calculate the vertical distance from each dot to the line
(the residual), square each of those 16 residuals, and then sum the 16 squared
residuals. The line for which the sum is the smallest is the “least squares” line,
and the parameter values
ˆ
θ
0
and
ˆ
θ
1
of this “least squares” line are the “least
squares” estimates. The values
ˆ
θ
0
and
ˆ
θ
1
can be easily computed using linear
algebra, as described in any statistics textbook.
In our example, the parameter estimates are
ˆ
θ
0
= 24.55 and
ˆ
θ
1
= 2.14,code: Program 11.2
Under the assumption that the vari-
ance of the residuals does not de-
pend on A (homoscedasticity), the
Wald 95% confidence intervals are
(−21.2, 70.3) for θ
0
, (1.28, 2.99)
for θ
1
, and (172.1, 261.6) for
E[Y |A = 90].
which define the straight line shown in Figure 11.4. The predicted mean of
Y among individuals with treatment level A = 90 is therefore
b
E[Y |A = 90] =
24.55 + 90 × 2.14 = 216.9. Because ordinary least squares estimation uses all
data points to find the best line, the mean of Y in the group A = a, i.e.,
E[Y |A = a], is estimated by borrowing information from individuals who have
values of treatment A not equal to a.
So what is a model? A model is defined by an a priori restriction on the
joint distribution of the data. Our linear conditional mean model says that the
conditional mean function E[Y |A] is a straight line, which restricts its shape.
For example, the model restricts the mean of Y for A = 90 to be between the
mean of Y for A = 80 and the mean of Y for A = 100. This restriction is
encoded by the parameters θ
0
and θ
1
. A parametric conditional mean model
150 Why model?
is, through its a priori restrictions, adding information to compensate for the
lack of sufficient information in the data.
Parametric estimators—those based on a parametric conditional mean model—
allow us to estimate quantities that cannot be estimated otherwise, e.g., the
mean of Y among individuals in the target population with treatment level
A = 90 when no such individuals exist in the study population. But this is not
a free lunch. When using a parametric model, the inferences are correct only
if the restrictions encoded in the model are correct, i.e. if the model is cor-
rectly specified. Thus model-based causal inference—to which a large fraction
of the remainder of this book is devoted—relies on the condition of (approx-
imately) no model misspecification. Because parametric models are rarely, if
ever, perfectly specified, a certain degree of model misspecification is almost al-
ways expected. This can be at least partially rectified by using nonparametric
estimators, which we describe in the next section.
11.3 Nonparametric estimators of the conditional mean
Let us return to the data in Figure 11.1. Treatment A is dichotomous and we
want to consistently estimate the mean of Y in the treated E[Y |A = 1] and in
the untreated E[Y |A = 0]. Suppose we have become so enamored with models
that we decide to use one to estimate these two quantities. Again we proposed
a linear model
E[Y |A] = θ
0
+ θ
1
A
where E[Y |A = 0] = θ
0
+ 0 ×θ
1
= θ
0
and E[Y |A = 1] = θ
0
+ 1 ×θ
1
= θ
0
+ θ
1
.
We use the least squares method to obtain estimates of the parameters θ
0
and
θ
1
. These estimates are
ˆ
θ
0
= 67.5 and
ˆ
θ
1
= 78.75. We therefore estimatecode: Program 11.2
b
E[Y |A = 0] = 67.5 and
b
E[Y |A = 1] = 146.25. Note that our model-based
estimates of the mean of Y are identical to the sample averages we calculated
in Section 11.1. This is not a coincidence but an expected finding.In this book we define “model”
as an a priori mathematical re-
striction on the possible states of
nature (Robins, Greenland 1986).
Part I was entitled “Causal infer-
ence without models” because it
only described saturated models.
Let us take a second look at the model E[Y |A] = θ
0
+ θ
1
A with a dichoto-
mous treatment A. If we rewrite the model as E[Y |A = 1] = E[Y |A = 0] + θ
1
,
we see that the model simply states that the mean in the treated E[Y |A = 1]
is equal to the mean in the untreated E[Y |A = 0] plus a quantity θ
1
, where θ
1
may be negative, positive or zero. But this statement is of course always true!
The model imposes no restrictions whatsoever on the values of E[Y |A = 1]
and E[Y |A = 0]. Therefore E[Y |A = a] = θ
0
+ θ
1
A with a dichotomous treat-
ment A is not a model because it lets the data speak for themselves, just like
the sample average does. “Models” which do not impose restrictions on the
distribution of the data are saturated models. Because they formally look like
models even if they do not fit our definition of model, saturated models are
ordinarily referred to as models too.
Generally, the model is saturated whenever the number of parameters in a
conditional mean model is equal to the number of unknown conditional means
in the population. For example, the linear model E[Y |A] = θ
0
+ θ
1
A has two
parameters and, when A is dichotomous, there exist two unknown conditional
means: the means E[Y |A = 1] and E[Y |A = 0]. Since the values of the two
parameters are not restricted by the model, neither are the values of the means.A saturated model has the same
number of unknowns on both sides
of the equal sign.
As a contrast, consider the data in Figure 11.3 where A can take values from 0
to 100. The linear model E[Y |A] = θ
0
+ θ
1
A has two parameters but estimates
101 quantities, i.e., E[Y |A = 0], E[Y |A = 1], ..., E[Y |A = 100]. The only hope
11.4 Smoothing 151
Fine Point 11.1
Fisher consistency. Our definition of a nonparametric estimator in the main text coincides with what is known in
statistics as a Fisher consistent estimator (Fisher 1922). That is, an estimator of a population quantity that, when
calculated using the entire population rather than a sample, yields the true value of the population parameter. By
definition, a Fisher consistent estimator lacks any model restrictions but, as discussed in the text, a Fisher consistent
estimate may not exist for many population quantities. Technically, Fisher consistent estimators, when they exist, are
the nonparametric maximum likelihood estimators of population quantities under a saturated model.
In the statistical literature, the term nonparametric estimator is sometimes used to refer to estimators that are not
Fisher consistent but that impose very weak restrictions, such as kernel regression models. See Technical Point 11.1 for
details.
for unbiasedly estimating 101 quantities with these two parameters is to be
fortunate to have all 101 means E[Y |A = a] lie along a straight line. When a
model has only a few parameters but it is used to estimate many population
quantities, we say that the model is parsimonious.
Here we define nonparametric estimators of the conditional mean function
as those that produce estimates from the data without any a priori restrictions
on the conditional mean function (see Fine Point 11.1 for a more rigorous def-Identifiability assumptions are the
assumptions that we have to make
to compute the parameter even if
we had an infinite amount of data.
Modeling assumptions are the ad-
ditional assumptions that we have
to make to estimate the parameter
because we do not have an infinite
amount of data. Formally, identi-
fiability assumptions make the pa-
rameter a unique function of the
joint distribution of the observed
data.
inition). An example of a nonparametric estimator of the population mean
E[Y |A = a] for a dichotomous treatment is its empirical version, the sample
average or, equivalently, the saturated model described in this section. When
A is discrete with 100 levels and no individual in the sample has A = 90, no
nonparametric estimator of E[Y |A = 90] exists. All methods for causal infer-
ence that we described in Part I of this book—standardization, IP weighting,
stratification, matching—were based on nonparametric estimators of popula-
tion quantities under a saturated model because they did not impose any a
priori restrictions on the value of the effect estimates. In contrast, most meth-
ods for causal inference described in Part II of this book rely on estimators
that are parametric estimators of some part of the distribution of the data.
Parametric estimation is one approach used to borrow information when, as is
often the case, data are unable to speak for themselves.
11.4 Smoothing
Consider again the data in Figure 11.3 and the linear model E[Y |A] = θ
0
+θ
1
A.
The parameter θ
1
is the difference in mean outcome per unit of treatment dose
A. Because θ
1
is a single number, the model specifies that the difference in
mean outcome Y per unit of treatment A must be constant throughout the
entire range of A, i.e., the model requires the conditional mean outcome to
follow a straight line as a function of treatment dose A. Figure 11.4 shows theCaution: Often the term “linear”
is used with two different mean-
ings. A model is linear when it is
expressed as a linear combination
of parameters and functions of the
variables, even if the latter are non-
linear functions (e.g., higher powers
or logarithms) of the covariates.
best-fitting straight line.
But one can imagine situations in which the difference in mean outcome is
larger for a one-unit change at low doses of treatment, and smaller for a one-
unit change at high doses. This would be the case if, once the treatment dose
reaches certain level, higher doses have an increasingly small effect. Under this
scenario, the model E[Y |A] = θ
0
+ θ
1
A is incorrect. However, linear models
can be made more flexible.
152 Why model?
For example, suppose we fit the model E[Y |A] = θ
0
+ θ
1
A + θ
2
A
2
, where
A
2
= A × A is A-squared, to the data in Figure 11.3. This is still referred
to as a linear model because the conditional mean is expressed as a linear
combination, i.e., as the sum of the products of each covariate (A and A
2
)
with its associated coefficient (the parameters θ
1
and θ
2
) plus an intercept
(θ
0
). However, whenever θ
2
is not zero, (θ
0
, θ
1
, θ
2
) now define a curve—a
parabola—rather than a straight line. We refer to θ
1
as the parameter for the
linear term A, and to θ
2
as the parameter for the quadratic term A
2
.
The curve under the 3-parameter linear model E[Y |A] = θ
0
+ θ
1
A + θ
2
A
2
can be found via ordinary least squares estimation applied to the data in
Figure 11.3. The estimated curve is shown in Figure 11.5. The parameter
estimates are
ˆ
θ
0
= −7.41,
ˆ
θ
1
= 4.11, and
ˆ
θ
2
= −0.02. The predicted meancode: Program 11.3
Under the homoscedasticity as-
sumption, the Wald 95% confi-
dence interval for
b
E[Y |A = 90] is
(142.8, 251.5).
of Y among individuals with treatment level A = 90 is obtained from the
expression
b
E[Y |A = 90] =
ˆ
θ
0
+ 90
ˆ
θ
1
+ 90 × 90
ˆ
θ
2
= 197.1.
We could keep adding parameters for a cubic term (θ
3
A
3
), a quartic term
(θ
4
A
4
)... until we reach a 15th-degree term (θ
15
A
15
). At that point the number
of parameters in our model equals the number of data points (individuals). The
shape of the curve would change as the number of parameters increases. In
general, the more parameters in the model, the more inflection points will
appear.
That is, the curve generally becomes more “wiggly,” or less smooth, as the
number of parameters increase. A linear model with 2 parameters—a straight
line—is the smoothest model. A linear model with as many parameters as data
points is the least smooth model because it has as many possible inflection
points as data points. In fact, such model interpolates the data, i.e., each data
point in the sample lies on the estimated conditional mean function.
Figure 11.5
Often modeling can be viewed as a procedure to transform noisy data into
more or less smooth curves. This smoothing occurs because the model borrows
information from many data points to predict the outcome value at a particular
combination of values of the covariates. The smoothing results from E[Y |A =
a] being estimated by borrowing information from individuals with A not equal
to a. All parametric estimators incorporate some degree of smoothing.
The degree of smoothing depends on how much information is borrowed
across individuals. The 2-parameter model E[Y |A] = θ
0
+ θ
1
A estimates
E[Y |A = 90] by borrowing information from all individuals in the study popu-
lation to find the least squares straight line. A model with as many parameters
as individuals does not borrow any information to estimate E[Y |A] at the values
of A that occur in the data, though it borrows information (by interpolation)
for values of A that do not occur in the data.
Intermediate degrees of smoothing can be achieved by using an intermediate
number of parameters or, more generally, by restricting the number of individ-
uals that contribute to the estimation. For example, to estimate E[Y |A = 90]We used a model for continuous
outcomes as an example. The same
reasoning applies to models for di-
chotomous outcomes such as lo-
gistic models (see Technical Point
11.1)
we could decide to fit a 2-parameter model E[Y |A] = θ
0
+ θ
1
A restricted to
individuals with treatment doses between 80 and 100. That is, we would only
borrow information from individuals in a 10-unit window of A = 90. The wider
the window around A = 90, the more smoothing would be achieved.
In our simplistic examples above, all models included a single covariate
(with either a single parameter for A or two parameters for A and A
2
) so that
the curves can be represented on a two-dimensional book page. In realistic
applications, models often include many different covariates so that the curves
are really hyperdimensional surfaces. Regardless of the dimensionality of the
problem, the concept of smoothing remains invariant: the fewer parameters in
the model, the smoother the prediction (response) surface will be.
11.5 The bias-variance trade-off 153
Fine Point 11.2
Model dimensionality and the relation between frequentist and Bayesian intervals. In frequentist statistical
inference, probability is defined as frequency. In Bayesian inference, probability is defined as degree-of-belief—a concept
very different from probability as frequency (de Finetti 1972). Chapter 10 described the confidence intervals used
in frequentist statistical inference. Bayesian statistical inference uses credible intervals, which have a more natural
interpretation: A Bayesian 95% credible interval means that, given the observed data, “there is a 95% probability that
the estimand is in the interval”. However, in part because of the requirement to specify the investigators’ degree of
belief, Bayesian inference is less commonly used than frequentist inference.
Interestingly, in simple, low-dimensional parametric models with large sample sizes, 95% Bayesian credible intervals
are also 95% frequentist confidence intervals, whereas in high-dimensional or nonparametric models, a Bayesian 95%
credible interval may not be a 95% confidence interval as it may trap the estimand much less than 95% of the time.
The underlying reason for these results is that Bayesian inference requires the specification of a prior distribution for
all unknown parameters. In low-dimensional parametric models the information in the data swamps that contained in
reasonable priors. As a result, inference is relatively insensitive to the particular prior distribution selected. However,
this is no longer the case in high-dimensional models. Therefore if the true parameter values that generated the data
are unlikely under the chosen prior distribution, the center of Bayes credible interval will be pulled away from the true
parameters and towards the parameter values given the greatest probability under the prior.
11.5 The bias-variance trade-off
In previous sections we have used the 16 individuals in Figure 11.3 to estimate
the mean outcome Y among people receiving a treatment dose of A = 90 in
the target population, E[Y |A = 90]. Since nobody in the study population
received A = 90, we could not let the data speak for themselves. So we
combined the data with a linear model. The estimate
b
E[Y |A = 90] varied with
the model. Under the 2-parameter model E[Y |A] = θ
0
+ θ
1
A, the estimate
was 216.9 (95% confidence interval: 172.1, 261.6). Under the 3-parameter
model E[Y |A] = θ
0
+ θ
1
A + θ
2
A
2
, the estimate was 197.1 (95% confidence
interval: 142.8, 251.5). We used two different parametric models that yielded
two different estimates. Which one is better? Is 216.9 or 197.1 closer to the
mean in the target population?
If the relation is truly curvilinear, then the estimate from the 2-parameter
model will be biased because this model assumes a straight line. On the other
hand, if the relation is truly a straight line, then the estimates from both models
will be valid. This is so because the 3-parameter model E[Y |A] = θ
0
+ θ
1
A +
θ
2
A
2
is correctly specified whether the relation follows a straight line (in which
case θ
2
= 0) or a parabolic curve (in which case θ
2
= 0). One safe strategy
would be to use the 3-parameter model E[Y |A] = θ
0
+ θ
1
A + θ
2
A
2
rather than
the 2-parameter model E[Y |A] = θ
0
+ θ
1
A. Because the 3-parameter model is
correctly specified under both a straight line and a parabolic curve, it is less
likely to be biased. In general, the larger the number of parameters in the
model, the fewer restrictions the model imposes; the less smooth the model,
the more protection afforded against bias from model misspecification.
Although less smooth models may yield a less biased estimate, they also
result in a larger variance, i.e., wider 95% confidence intervals around the
estimate. For example, the estimated 95% confidence interval around
b
E[Y |A =
90] was much wider when we used the 3-parameter model than when we used
the 2-parameter model. However, when the estimate
b
E[Y |A = 90] based on the
2-parameter model is biased, the standard (nominal) 95% confidence interval
154 Why model?
is not calibrated, i.e., it does not cover the true parameter E[Y |A = 90] 95%
of the time.Fine Point 11.2 discusses the impli-
cations of model dimensionality for
frequentist and Bayesian intervals.
This bias-variance trade-off is at the heart of many data analyses. Investi-
gators using models need to decide whether some protection against bias—by,
say, adding more parameters to the model—is worth the cost in terms of vari-
ance. Though some formal procedures exist to aid these decisions, in practice
many investigators decide which model to use based on criteria like tradition,
interpretability of the parameters, and software availability. In this book we
will usually assume that our parametric models are correctly specified. This
is an unrealistic assumption, but it allows us to focus on the problems that
are specific to causal analyses. Model misspecification is, after all, a problem
that can arise in any sort of data analysis, regardless of whether the estimates
are endowed with a causal interpretation. In practice, careful investigators
will always question the validity of their models and will conduct alternative
analysis under different model specifications that are compatible with existing
expert knowledge. Their goal is to assess the sensitivity of their estimates to
model specification.
We are now ready to describe the use of models for causal inference.
11.5 The bias-variance trade-off 155
Technical Point 11.1
A taxonomy of commonly used models. The main text describes linear conditional mean models of the form
E[Y |X] = θX ≡
p
P
i=0
θ
i
X
i
where X is a vector of covariates X
0
, X
1
, ...X
p
with X
0
= 1 for all n individuals. These
models are a subset of larger class of conditional mean models (McCullagh and Nelder, 1989; McCulloch, Searle, and
Neuhaus, 2008) which have two components: a linear functional form or predictor
p
P
i=0
θ
i
X
i
and a link function g {·}
such that g {E[Y |X]} =
p
P
i=1
θ
i
X
i
.
The linear conditional mean models described in the main text uses the identity link function. Conditional mean models
for outcomes with strictly positive values (e.g., counts, the numerator of incidence rates) often use the log link function
to ensure that all predicted values will be greater than zero, i.e., log {E[Y |X]} =
p
P
i=0
θ
i
X
i
so E[Y |X] = exp
p
P
i=0
θ
i
X
i
.
Conditional mean models for dichotomous outcomes (i.e., those that only take values 0 and 1) often use a logit link
i.e., log
n
E[Y |X]
1−E[Y |X]
o
=
p
P
i=0
θ
i
X
i
, so that E[Y |X] = expit
p
P
i=0
θ
i
X
i
. This link ensures that all predicted values will be
greater than 0 and less than 1. Conditional mean models that use the logit function, referred to as logistic regression
models, are widely used in this book. For these links (referred to as canonical links) we can estimate θ by maximum
likelihood under a normal working model for the identity link, a Poisson working model for the log link, and a logistic
regression model for the logit link. These estimates are consistent for θ as long as the conditional mean model for
E[Y |X] is correct. Generalized estimating equation (GEE) models, often used to deal with repeated measures, are a
further example of a conditional mean model (Liang and Zeger, 1986).
Conditional mean models only specify a parametric form for E[Y |X] but do not otherwise restrict the distribution of
Y |X or the marginal distribution of X. Therefore, when X or Y are continuous, a parametric conditional mean model
is a semiparametric model for the joint distribution of the data (X, Y ) because parts of the distribution are modeled
parametrically whereas others are left unrestricted. The model is semiparametric because the set of all unrestricted
components of the joint distribution cannot be represented by a finite number of parameters.
Conditional mean models themselves can be generalized by relaxing the assumption that E[Y |X] takes a parametric
form. For example, a kernel regression model does not impose a specific functional form on E[Y |X] but rather estimates
E[Y |X = x] for any x by
n
P
i=1
w
h
(x − X
i
) Y
i
/
n
P
i=1
w
h
(x − X
i
) where w
h
(z) is a positive function, known as a kernel
function, that attains its maximum value at z = 0 and decreases to 0 as |z| gets large at a rate that depends on the
parameter h subscripting w. As another example, generalized additive models (GAMs) replace the linear combination
p
P
i=0
θ
i
X
i
of a conditional mean model by a sum of smooth functions
p
P
i=0
f
i
(X
i
). The model can be estimated using a
backfitting algorithm with f
i
(·) estimated at iteration k by, e.g., kernel regression (Hastie and Tibshirani 1990).
In the text we discuss smoothing with parametric models which specify an a priori functional form for E[Y |X = x],
such as a parabola. In estimating E [Y |X = x], the model may borrow information from values of X that are far from
x. In contrast, kernel regression models do not specify an a priori functional form and borrow information only from
values of X near to x when estimating E [Y |X = x]. A kernel regression model is an example of a “non-parametric”
regression model. This use of the term “nonparametric” differs from our previous usage. Our nonparametric estimators
of E [Y |X = x] only used those individuals for whom X equalled x exactly; no information was borrowed even from
close neighbors. Here “nonparametric” estimators of E [Y |X = x] use individuals with values of X near to x. How near
is controlled by a smoothing parameter referred to as the bandwidth h.
156 Why model?
Chapter 12
IP WEIGHTING AND MARGINAL STRUCTURAL MODELS
Part II is organized around the causal question “what is the average causal effect of smoking cessation on body
weight gain?” In this chapter we describe how to use IP weighting to estimate this effect from observational data.
Though IP weighting was introduced in Chapter 2, we only described it as a nonparametric method. We now
describe the use of models together with IP weighting which, under additional assumptions, will allow us to tackle
high-dimensional problems with many covariates and nondichotomous treatments.
To estimate the effect of smoking cessation on weight gain we will use real data from the NHEFS, an acronym
that stands for (ready for a long name?) National Health and Nutrition Examination Survey Data I Epidemi-
ologic Follow-up Study. The NHEFS was jointly initiated by the National Center for Health Statistics and the
National Institute on Aging in collaboration with other agencies of the United States Public Health Service. A
detailed description of the NHEFS, together with publicly available data sets and documentation, can be found at
wwwn.cdc.gov/nchs/nhanes/nhefs/. For this and future chapters, we will use a subset of the NHEFS data that
is available from this book’s web site. We encourage readers to improve upon and refine our analyses.
12.1 The causal question
Our goal is to estimate the average causal effect of smoking cessation (the
treatment) A on weight gain (the outcome) Y . To do so, we will use data
from 1566 cigarette smokers aged 25-74 years who, as part of the NHEFS, hadWe restricted the analysis to indi-
viduals with known sex, age, race,
weight, height, education, alcohol
use and intensity of smoking at
the baseline (1971-75) and follow-
up (1982) visits, and who answered
the medical history questionnaire at
baseline. See Fine Point 12.1.
a baseline visit and a follow-up visit about 10 years later. Individuals were
classified as treated A = 1 if they reported having quit smoking before the
follow-up visit, and as untreated A = 0 otherwise. Each individual’s weight
gain Y was measured (in kg) as the body weight at the follow-up visit minus
the body weight at the baseline visit. Most people gained weight, but quitters
gained more weight on average. The average weight gain was
b
E[Y |A = 1] = 4.5
kg in the quitters, and
b
E[Y |A = 0] = 2.0 kg in the non-quitters. The difference
E[Y |A = 1] − E[Y |A = 0] was therefore estimated to be 2.5, with a 95%
confidence interval from 1.7 to 3.4.
We define E[Y
a=1
] as the mean weight gain that would have been observed
if all individuals in the population had quit smoking before the follow-up visit,Table 12.1
Mean baseline A
characteristics 1 0
Age, years 46.2 42.8
Men, % 54.6 46.6
White, % 91.1 85.4
University, % 15.4 9.9
Weight, kg 72.4 70.3
Cigarettes/day 18.6 21.2
Years smoking 26.0 24.1
Little exercise, % 40.7 37.9
Inactive life, % 11.2 8.9
and E[Y
a=0
] as the mean weight gain that would have been observed if all
individuals in the population had not quit smoking. We define the average
causal effect on the additive scale as E[Y
a=1
] − E[Y
a=0
], i.e., the difference
in mean weight that would have been observed if everybody had been treated
compared with untreated. This is the causal effect that we will be primarily
concerned with in this and the next chapters.
The associational difference E[Y |A = 1] − E[Y |A = 0], which we estimated
in the first paragraph of this section, is generally different from the causal
difference E[Y
a=1
] − E[Y
a=0
]. The former will not generally have a causal
interpretation if quitters and non-quitters differ with respect to characteristics
that affect weight gain. For example, quitters were on average 4 years older
than non-quitters (quitters were 44% more likely to be above age 50 than non
158 IP weighting and marginal structural models
Fine Point 12.1
Setting a bad example. Our smoking cessation example is convenient: it does not require deep subject-matter
knowledge and the data are publicly available. One price we have to pay for this convenience is potential selection bias.
We classified individuals as treated A = 1 if they reported (i) being smokers at baseline in 1971-75, and (ii) having
quit smoking in the 1982 survey. Condition (ii) implies that the individuals included in our study did not die and were
not otherwise lost to follow-up between baseline and 1982 (otherwise they would not have been able to respond to the
survey). That is, we selected individuals into our study conditional on an event—responding the 1982 survey—that
occurred after the start of the treatment—smoking cessation. If treatment affects the probability of selection into the
study, we might have selection bias as described in Chapter 8. (Because different individuals quit smoking at different
times, A is actually a time-varying treatment, which we will ignore throughout Part II. Time-varying treatments are
discussed in Part III.)
A randomized experiment of smoking cessation would not have this problem. Each individual would be assigned to
either smoking cessation or no smoking cessation at baseline, so that their treatment group would be known even if the
individual did not make it to the 1982 visit. In Section 12.6 we describe how to deal with potential selection bias due
to censoring or missing data for the outcome—something that may occur in both observational studies and randomized
experiments—but the situation described in this Fine Point is different: the missing data concerns the treatment itself.
This selection bias can be handled through sensitivity analysis, as was done by Hern´an et al. (2008, Appendix 3).
The choice of this example allows us to describe, in our own analysis, a ubiquitous problem in published analyses of
observational data that emulate a target trial: a misalignment of treatment assignment and eligibility at the start of
follow-up (Hern´an et al. 2016). Though we decided to ignore this issue in order to keep our analysis simple, didactic
convenience would not be a good excuse to avoid dealing with this bias in real life.
quitters), and older people gained less weight than younger people, regardless
of whether they did or did not quit smoking. We say that age is a (surrogate)Fine Point 7.3 defined surrogate
confounders. confounder of the effect of A on Y and our analysis needs to adjust for age. The
unadjusted estimate 2.5 might underestimate the true causal effect E[Y
a=1
] −
E[Y
a=0
].
As shown in Table 12.1, quitters and non-quitters also differed in their dis-code: Program 12.1 computes the
descriptive statistics shown in this
section
tribution of other variables such as sex, race, education, baseline weight, and
intensity of smoking. If these variables are confounders, then they also need
to be adjusted for in the analysis. In Chapter 18 we discuss strategies for con-
founder selection. Here we assume that the following 9 variables, all measured
at baseline, are sufficient to adjust for confounding: sex (0: male, 1: female),
age (in years), race (0: white, 1: other), education (5 categories), intensity
and duration of smoking (number of cigarettes per day and years of smoking),
physical activity in daily life (3 categories), recreational exercise (3 categories),
and weight (in kg). That is, L represents a vector of 9 measured covariates.
In the next section we use IP weighting to adjust for these covariates.
12.2 Estimating IP weights via modeling
IP weighting creates a pseudo-population in which the arrow from the covari-
ates L to the treatment A is removed. More precisely, the pseudo-population
has the following two properties: A and L are statistically independent and
the mean E
ps
[Y |A = a] in the pseudo-population equals the standardized mean
P
l
E[Y |A = a, L = l] Pr [L = l] in the actual population. These properties are
true even if conditional exchangeability Y
a
⊥⊥A|L does not hold in the ac-
12.2 Estimating IP weights via modeling 159
tual population (see Technical Point 2.3). Now, if conditional exchangeability
Y
a
⊥⊥A|L holds in the actual population, then these properties imply that (i)
the mean of Y
a
is the same in both populations, (ii) unconditional exchange-
ability (i.e., no confounding) holds in the pseudo-population, (iii) the counter-
factual mean E[Y
a
] in the actual population is equal to E
ps
[Y |A = a] in the
pseudo-population, and (iv) association is causation in the pseudo-population.
Please reread Chapter 2 if you need a refresher on IP weighting.
Informally, the pseudo-population is created by weighting each individual
by the inverse (reciprocal) of the conditional probability of receiving the treat-
ment level that she indeed received. The individual-specific IP weights for
treatment A are defined as W
A
= 1/f (A|L). For our dichotomous treat-
ment A, the denominator f (A|L) of the IP weight is the probability of quit-
ting conditional on the measured confounders, Pr [A = 1|L], for the quitters,The conditional probability of treat-
ment Pr [A = 1|L] is known as
the propensity score. More about
propensity scores in Chapter 15.
and the probability of not quitting conditional on the measured confounders,
Pr [A = 0|L], for the non-quitters. We only need to estimate Pr [A = 1|L] be-
cause Pr [A = 0|L] = 1 − Pr [A = 1|L].
In Section 2.4 we estimated the quantity Pr [A = 1|L] nonparametrically:
we simply counted how many people were treated (A = 1) in each stratum of
L, and then divided this count by the number of individuals in the stratum.
All the information required for this calculation was taken from a causally in-
terpreted structured tree graph with 4 branches (2 for L times 2 for A). But
nonparametric estimation of Pr [A = 1|L] is out of the question when, as in
our example, we have high-dimensional data with many confounders, some of
them with many levels. Even if we were willing to recode all 9 confoundersThe curse of dimensionality was in-
troduced in Chapter 10. except age to a maximum of 6 categories each, our tree would still have over 2
million branches. And many more millions if we use the actual range of values
of duration and intensity of smoking, and weight. We cannot obtain meaning-
ful nonparametric stratum-specific estimates when there are 1566 individuals
distributed across millions of strata. We need to resort to modeling.
To obtain parametric estimates of Pr [A = 1|L] in each of the millions of
strata defined by L, we fit a logistic regression model for the probability of
quitting smoking with all 9 confounders included as covariates. We used linear
and quadratic terms for the (quasi-)continuous covariates age, weight, inten-
sity and duration of smoking, and we included no product terms between the
covariates. That is, our model restricts the possible values of Pr [A = 1|L] such
that, on the logit scale, the conditional relation between the continuous covari-
ates and the risk of quitting can be represented by a parabolic curve, and each
covariate’s contribution to the (logit of the) risk is independent of that of the
other covariates. Under these parametric restrictions, we were able to obtaincode: Program 12.2
The estimated IP weights W
A
ranged from 1.05 to 16.7, and their
mean was 2.00.
an estimate
c
Pr [A = 1|L] for each combination of L values, and therefore for
each of the 1566 individuals in the study population.
The next step is computing the difference
b
E
ps
[Y |A = 1] −
b
E
ps
[Y |A = 0]
in the pseudo-population created by the estimated IP weights. If there is
no confounding for the effect of A in the pseudo-population and the model
for Pr [A = 1|L] is correct, association is causation and an unbiased estimator
of the associational difference E
ps
[Y |A = 1] − E
ps
[Y |A = 0] in the pseudo-E[Y |A] = θ
0
+ θ
1
A is a saturated
model because it has 2 parameters,
θ
0
and θ
1
, to estimate two quanti-
ties, E[Y |A = 1] and E[Y |A = 0].
In this model, θ
1
= E[Y |A = 1] −
E[Y |A = 0].
population is also an unbiased estimator of the causal difference E[Y
a=1
] −
E[Y
a=0
] in the actual population.
Our approach to estimate E
ps
[Y |A = 1] − E
ps
[Y |A = 0] in the pseudo-
population was to fit the (saturated) linear mean model E[Y |A] = θ
0
+ θ
1
A
by weighted least squares, with individuals weighted by their estimated IP
weights
c
W : 1/
c
Pr [A = 1|L] for the quitters, and 1/
1 −
c
Pr [A = 1|L]
for the
160 IP weighting and marginal structural models
Technical Point 12.1
Horvitz-Thompson estimators. In Technical Point 3.1, we defined the “apparent” IP weighted mean for treatment
level a, E
I (A = a) Y
f (A|L)
, which is equal to the counterfactual mean E[Y
a
] under positivity and exchangeability. This
IP weighted mean is consistently estimated by the original Horvitz-Thompson (1952) estimator
b
E
I (A = a) Y
f (A|L)
with
b
E the sample average operator and f (A|L) assumed to be known. In this chapter, however, we estimated E[Y
a
] via
the IP weighted least squares estimate
ˆ
θ
0
+
ˆ
θ
1
a, which for binary A is a modified Horvitz-Thompson estimator often
referred to as Hajek estimator
b
E
I (A = a) Y
f (A|L)
b
E
I (A = a)
f (A|L)
(Hajek 1971).
The Hajek estimator is an (asymptotically) unbiased estimator of
E
I (A = a) Y
f (A|L)
E
I (A = a)
f (A|L)
which, under positivity, is equal
to E
I (A = a) Y
f (A|L)
because E
I (A = a)
f (A|L)
= 1. In practice, the Hajek estimator is preferred because, unlike the
Horvitz-Thompson estimator, it is guaranteed to lie between 0 and 1 for dichotomous Y , even when f (A|L) is unknown
and replaced by the predicted value
ˆ
f (A|L) obtained from the fit of a misspecified model.
On the other hand, if positivity does not hold, then the ratio
E
I (A = a) Y
f (A|L)
E
I (A = a)
f (A|L)
equals
P
l
E [Y |A = a, L = l, L ∈ Q(a)] Pr [L = l|L ∈ Q(a)] and, if exchangeability holds, it equals E [Y
a
|L ∈ Q(a)],
where Q(a) = {l; Pr (A = a|L = l) > 0} is the set of values l for which A = a may be observed with positive
probability. Therefore, as discussed in Technical Point 3.1, the difference between Hajek estimators with a = 1 versus
a = 0 does not have a causal interpretation in the absence of positivity. Under non-positivity, the ratio of the limit of
the Horvitz-Thompson estimator to that of the Hajek estimator is no longer 1 but rather Pr [Q(a)], as the denominator
of the Hajek estimator converges to Pr [Q(a)] rather to 1.
non-quitters. The parameter estimate
ˆ
θ
1
was 3.4. That is, we estimated that
quitting smoking increases weight by
ˆ
θ
1
= 3.4 kg on average. See Technical
Point 12.1 for a formal definition of the estimator.The weighted least squares esti-
mates
ˆ
θ
0
and
ˆ
θ
1
with weight W
of θ
0
and θ
1
are the minimizers
of
P
i
c
W
i
[Y
i
− (θ
0
+ θ
1
A
i
)]
2
. If
c
W
i
= 1 for all individuals i, we ob-
tain the ordinary least squares es-
timates described in the previous
chapter.
To obtain a 95% confidence interval around the point estimate
ˆ
θ
1
= 3.4
we need a method that takes the IP weighting into account. One possibil-
ity is to use statistical theory to derive the corresponding variance estimator.
This approach requires that the data analyst programs the estimator, which
is not generally available in standard statistical software. A second possibility
is to approximate the variance by nonparametric bootstrapping. This ap-
proach requires appropriate computing resources, or lots of patience, for large
databases. A third possibility is to use the robust variance estimator (e.g., as
used for GEE models with an independent working correlation) that is a stan-
dard option in most statistical software packages. The 95% confidence intervals
based on the robust variance estimator are valid but, unlike the above analytic
and bootstrap estimators, conservative—they cover the super-population pa-
rameter more than 95% of the time. The conservative 95% confidence interval
around
ˆ
θ
1
was (2.4, 4.5). In this chapter, all confidence intervals for IP weighted
12.3 Stabilized IP weights 161
estimates are conservative. If the model for Pr [A = 1|L] is misspecified, the
estimates of θ
0
and θ
1
will be biased and, like we discussed in the previous
chapter, the confidence intervals may cover the true values less than 95% of
the time.
12.3 Stabilized IP weights
The goal of IP weighting is to create a pseudo-population in which there is
no association between the covariates L and treatment A. In Chapter 2 we
showed how the original study population in Figure 2.1 was transformed into
the pseudo-population in Figure 2.3 by using the IP weights W
A
= 1/f (A|L).
The size of the pseudo-population is twice that of the original study population,
which reflects the fact that the average of the weights W
A
is 2. Informally,
the weights simulate a pseudo-population that is formed by two copies of the
original study population, one of which is treated and the other untreated.
However, there are other ways to create a pseudo-population in which A and
L are independent. For example, a pseudo-population in which all individuals
have a probability of receiving A = 1 equal to 0.5 and a probability of receiving
A = 0 also equal to 0.5, regardless of their values of L. Such pseudo-population
is constructed by using IP weights 0.5/f (A|L). This pseudo-population would
be of the same size as the study population and it would be algebraically equal
to the pseudo-population of the previous paragraph if all weights are divided
by 2. Hence, the expected mean of the weights 0.5/f (A|L) is 1 and the effect
estimate obtained in the pseudo-population created by weights 0.5/f (A|L) is
equal to that obtained in the pseudo-population created by weights 1/f (A|L).
(You can check this empirically by using the data in Figure 2.1, or see the proof
in Technical Point 12.2.) The same goes for any other IP weights p/f (A|L)
with 0 < p ≤ 1. The weights W
A
= 1/f (A|L) are just one particular example
of IP weights with p = 1.
Let us take our reasoning a step further. The key requirement for confound-
ing adjustment is that, in the pseudo-population, the probability of treatment
A does not depend on the confounders L. We can achieve this requirement
by assigning treatment with the same probability p to everyone in the pseudo-
population. But we can also achieve it by creating a pseudo-population in
which different people have different probabilities of treatment, as long as the
probability of treatment does not depend on the value of L. For example, a
common choice is to assign to the treated the probability of receiving treatment
Pr [A = 1] in the original population, and to the untreated the probability of
not receiving treatment Pr [A = 0] in the original population. Thus the IPThe average causal effect in the
treated subpopulation can be esti-
mated by using IP weights in which
the numerator is Pr[A = 1|L]. See
Technical Point 4.1.
weights are Pr [A = 1] /f (A|L) for the treated and Pr [A = 0] /f (A|L) for the
untreated or, more compactly, f (A) /f (A|L).
Figure 12.1 shows the pseudo-population that is created by the IP weights
f (A) /f (A|L) when applied to the data in Figure 2.1, where Pr [A = 1] =
13/20 = 0.65 and Pr [A = 0] = 7/20 = 0.35. Under the identifiability condi-
tions of Chapter 3, the pseudo-population resembles a hypothetical randomized
experiment in which 65% of the individuals in the study population have been
randomly assigned to A = 1, and 35% to A = 0. Note that, to preserve
the 65/35 ratio, the number of individuals in each branch cannot be integers.
Fortunately, non-whole people are no big deal in mathematics.
In our smoking cessation example, the IP weights f (A) /f (A|L) range from
0.33 to 4.30, whereas the IP weights 1/f (A|L) range from 1.05 to 16.7. The
162 IP weighting and marginal structural models
stabilizing factor f (A) in the numerator is responsible for the narrower range
of the f (A) /f (A|L) weights. The IP weights W
A
= 1/f (A|L) are referred to
as nonstabilized weights, and the IP weights SW
A
= f (A) /f (A|L) are referred
to as stabilized weights. The mean of the stabilized weights is expected to be 1
because the size of the pseudo-population equals that of the study population.
Figure 12.1
Let us now re-estimate the effect of quitting smoking on body weight by
using the stabilized IP weights SW
A
. First, we need an estimate of the con-
ditional probability Pr [A = 1|L] to construct the denominator of the weights.In data analyses one should check
that the estimated weights SW
A
have mean 1 (Hern´an and Robins
2006a). Deviations from 1 indi-
cate model misspecification or pos-
sible violations, or near violations,
of positivity. See Fine Point 12.2
for more on checking positivity.
We use the same logistic model we used in Section 12.2 to obtain a parametric
estimate
c
Pr [A = 1|L] for each of the 1566 individuals in the study population.
Second, we need to estimate Pr [A = 1] for the numerator of the weights. We
can obtain a nonparametric estimate by the ratio 403/1566 or, equivalently,
by fitting a saturated logistic model for Pr [A = 1] with an intercept and no
covariates. Finally, we estimate the causal difference E[Y
a=1
] − E[Y
a=0
] by
fitting the mean model E[Y |A] = θ
0
+ θ
1
A with individuals weighted by their
estimated stabilized IP weights:
c
Pr [A = 1] /
c
Pr [A = 1|L] for the quitters, and
1 −
c
Pr [A = 1]
/
1 −
c
Pr [A = 1|L]
for the non-quitters. Under our assump-
tions, we estimated that quitting smoking increases weight by
ˆ
θ
1
= 3.4 kg (95%
confidence interval: 2.4, 4.5) on average. This is the same estimate we obtainedcode: Program 12.3
The estimated IP weights SW
A
ranged from 0.33 to 4.30, and their
mean was 1.00.
earlier using the nonstabilized IP weights W
A
rather than the stabilized IP
weights SW
A
.
If nonstabilized and stabilized IP weights result in the same estimate, why
use stabilized IP weights then? Because stabilized weights typically result in
narrower 95% confidence intervals than nonstabilized weights. However, the
statistical superiority of the stabilized weights can only occur when the (IP
weighted) model is not saturated. In our above example, the two-parameter
model E[Y |A] = θ
0
+ θ
1
A was saturated because treatment A could only take
2 possible values. In many settings (e.g., time-varying or continuous treat-
ments), the weighted model cannot possibly be saturated and therefore stabi-
12.4 Marginal structural models 163
Fine Point 12.2
Checking positivity. In our study, there are 4 white women aged 66 years and none of them quit smoking. That is, the
probability of A = 1 conditional on (a subset of) L is 0. Positivity, a condition for IP weighting, is empirically violated.
There are two possible ways in which positivity can be violated:
• Structural violations: The type of violations described in Chapter 3. Individuals with certain values of L cannot
possibly be treated (or untreated). An example: when estimating the effect of exposure to certain chemicals on
mortality, being off work is an important confounder because people off work are more likely to be sick and to die,
and a determinant of chemical exposure—people can only be exposed to the chemical while at work. That is, the
structure of the problem guarantees that the probability of treatment conditional on being off work is exactly 0
(a structural zero). We’ll always find zero cells when conditioning on that confounder.
• Random violations: The type of violations described in the first paragraph of this Fine Point. Our sample is finite
so, if we stratify on several confounders, we will start finding zero cells at some places even if the probability
of treatment is not really zero in the target population. This is a random, not structural, violation of positivity
because the zeroes appear randomly at different places in different samples of the target population. An example:
our study happened to include 0 treated individuals in the strata “white women age 66” and “white women age
67”, but it included a positive number of treated individuals in the strata “white women age 65” and “white
women age 69.”
Each type of positivity violation has different consequences. In the presence of structural violations, causal inferences
cannot be made about the entire population using IP weighting or standardization. The inference needs to be restricted
to strata in which structural positivity holds. See Technical Point 12.1 for details. In the presence of random violations,
we used our parametric model to estimate the probability of treatment in the strata with random zeroes using data
from individuals in the other strata. In other words, we use parametric models to smooth over the zeroes. For example,
the logistic model used in Section 12.2 estimated the probability of quitting in white women aged 66 by interpolating
from all other individuals in the study. Every time we use parametric estimation of IP weights in the presence of zero
cells—like we did in estimating
ˆ
θ
1
= 3.4—, we are effectively assuming random nonpositivity.
lized weights are used. The next section describes the use of stabilized weights
for a continuous treatment.
12.4 Marginal structural models
Consider the following linear model for the mean outcome under treatment
level aThis is a (saturated) marginal
structural mean model for a di-
chotomous treatment A.
E[Y
a
] = β
0
+ β
1
a
This model is different from all models we have described so far: the out-
come variable of this model is counterfactual—and hence generally unobserved.
Therefore the model cannot be fit to the data of any real-world study. Models
for the marginal mean of a counterfactual outcome are referred to as marginal
structural mean models.
The parameters for treatment in structural mean models correspond to
average causal effects. In the above model, the parameter β
1
is equal to
E[Y
a=1
] − E[Y
a=0
] because E[Y
a
] = β
0
under a = 0 and E[Y
a
] = β
0
+ β
1
under a = 1. In previous sections, we have estimated the average causal effect
of smoking cessation A on weight change Y defined as E[Y
a=1
] − E[Y
a=0
].
164 IP weighting and marginal structural models
In other words, we have estimated the parameter β
1
of a marginal structural
model.
Specifically, we used IP weighting to construct a pseudo-population, and
then fit the model E[Y |A] = θ
0
+ θ
1
A to the pseudo-population data by using
IP weighted least squares. Under our assumptions, association is causation
in the pseudo-population. That is, the parameter θ
1
from the IP weighted
associational model E[Y |A] = θ
0
+ θ
1
A can be endowed with the same causal
interpretation as the parameter β
1
from the structural model E[Y
a
] = β
0
+
β
1
a. It follows that a consistent estimate
ˆ
θ
1
of the associational parameter
in the pseudo-population is also a consistent estimator of the causal effect
β
1
= E[Y
a=1
] − E[Y
a=0
] in the population.
The marginal structural model E[Y
a
] = β
0
+ β
1
a is saturated because
smoking cessation A is a dichotomous treatment. That is, the model has 2
unknowns on both sides of the equation: E[Y
a=1
] and E[Y
a=0
] on the left-hand
side, and β
0
and β
1
on the right-hand side. Thus sample averages computed
in the pseudo-population were enough to estimate the causal effect of interest.A desirable property of marginal
structural models is null preserva-
tion (see Chapter 9): when the null
hypothesis of no average causal ef-
fect is true, a marginal structural
model is never misspecified. For ex-
ample, under this null hypothesis,
marginal structural model E[Y
a
] =
β
0
+β
1
a+β
2
a
2
is correctly specified
with β
1
= β
2
= 0 and β
0
= E[Y
a
]
for any a. If conditional exchange-
ability holds, then E[Y ] = β
0
.
But treatments are often polytomous or continuous. For example, con-
sider the new treatment A “change in smoking intensity” defined as number
of cigarettes smoked per day in 1982 minus number of cigarettes smoked per
day at baseline. Treatment A can now take many values such as −25 if an
individual decreased his number of daily cigarettes by 25, or 40 if an individ-
ual increased his number of daily cigarettes by 40. Let us say that we are
interested in estimating the difference in average weight change under different
changes in treatment intensity in the 1162 individuals who smoked 25 or fewer
cigarettes per day at baseline. That is, we want to estimate E[Y
a
] −E[Y
a
′
] for
any values a and a
′
.
Because treatment A can take dozens of values, a saturated model with
as many parameters becomes impractical. We will have to consider a non-
saturated structural model to specify the dose-response curve for the effect of
treatment A on the mean outcome Y . If we believe that a parabola appropri-
ately describes the dose-response curve, then we would propose the marginal
structural modelA (nonsaturated) marginal struc-
tural mean model for a continuous
treatment A.
E[Y
a
] = β
0
+ β
1
a + β
2
a
2
where a
2
= a × a is a-squared and E[Y
a=0
] = β
0
is the average weight gain
under a = 0, i.e., under no change in smoking intensity between baseline and
1982.
Suppose we want to estimate the average causal effect of increasing smoking
intensity by 20 cigarettes per day compared with no change, i.e., E[Y
a=20
] −
E[Y
a=0
]. According to our structural model, E[Y
a=20
] = β
0
+ 20β
1
+ 400β
2
,
and thus E[Y
a=20
] − E[Y
a=0
] = 20β
1
+ 400β
2
. Now we need to estimate the
parameters β
1
and β
2
. To do so, we need to estimate IP weights SW
A
to
create a pseudo-population in which there is no confounding by L, and then
fit the associational model E[Y |A] = θ
0
+ θ
1
A +θ
2
A
2
to the pseudo-populationcode: Program 12.4
The estimated SW
A
ranged from
0.19 to 5.10 with mean 1.00. We
assumed constant variance (ho-
moscedasticity), which seemed rea-
sonable after inspecting a residuals
plot. Other choices of distribution
(e.g., truncated normal with het-
eroscedasticity) resulted in similar
estimates.
data.
To estimate the stabilized weights SW
A
= f (A) /f (A|L) we need to esti-
mate f (A|L). For a dichotomous treatment A, f (A|L) is a probability so we
used a logistic model to estimate Pr [A = 1|L]. For a continuous treatment A,
f (A|L) is a probability density function (pdf). Unfortunately, pdfs are gener-
ally hard to estimate, particularly when L is high-dimensional with continuous
components, which is why using IP weighting for continuous treatments will
often be dangerous. In our example, we assumed that the density f (A|L) was
normal (Gaussian) with mean µ
L
= E[A|L] and constant variance σ
2
. We then
12.5 Effect modification and marginal structural models 165
used a linear regression model to estimate the mean E[A|L] and variance of
residuals σ
2
for all combinations of values of L. We also assumed that the
density f (A) in the numerator was normal. One should be careful when using
IP weighting for continuous treatments because the effect estimates may be
exquisitely sensitive to the choice of the model or algorithm used to estimateThe development of methods for
more stable estimation of IP
weights is an active area of re-
search. See the work by Imai and
Ratkovic (2015), Wang and Zu-
bizarreta (2020), Kallus and Santa-
catterina (2018), and Avagyan and
Vansteelandt (2021).
the conditional density f (A|L).
Our IP weighted estimates of the parameters of the marginal structural
model were
ˆ
β
0
= 2.005,
ˆ
β
1
= −0.109, and
ˆ
β
2
= 0.003. According to these
estimates, the mean weight gain (95% confidence interval) would have been 2.0
kg (1.4, 2.6) if all individuals had kept their smoking intensity constant, and
0.9 kg (−1.7, 3.5) if all individuals had increased smoking by 20 cigarettes/day
between baseline and 1982. The estimate of E[Y
a=20
] − E[Y
a=0
] is therefore
2.0 − 0.9 = 1.10 kg.
One can also consider a marginal structural model for a dichotomous out-
come. For example, if interested in the causal effect of quitting smoking A (1:
yes, 0: no) on the risk of death D (1: yes, 0: no) by 1992, one could consider
a marginal structural logistic model likeThis is a saturated marginal struc-
tural logistic model for a dichoto-
mous treatment. For a continuous
treatment, we would specify a non-
saturated logistic model.
logit Pr[D
a
= 1] = α
0
+ α
1
a
where exp (α
1
) is the causal odds ratio of death for quitting versus not quitting
smoking. The parameters of this model are consistently estimated, under our
assumptions, by fitting the logistic model logit Pr[D = 1|A] = θ
0
+ θ
1
A to
the pseudo-population created by IP weighting. We estimated the causal oddscode: Program 12.5
ratio to be exp
ˆ
θ
1
= 1.0 (95% confidence interval: 0.8, 1.4).
12.5 Effect modification and marginal structural models
Marginal structural models do not include covariates when the target param-
eter is the average causal effect in the population. However, one may include
covariates—which may be non-confounders—in a marginal structural model to
assess effect modification. Suppose it is hypothesized that the effect of smoking
cessation varies by sex V (0: male, 1: female). To examine this hypothesis, we
add the covariate V to our marginal structural mean model:
E [Y
a
|V ] = β
0
+ β
1
a + β
2
V a + β
3
V
Additive effect modification is present if β
2
= 0. Technically, this is not
a marginal model any more—because it is conditional on V —but the term
“marginal structural model” is still applied.The parameter β
3
does not gener-
ally have a causal interpretation as
the effect of V . Remember that we
are assuming exchangeability, pos-
itivity, and consistency for treat-
ment A, not for sex V.
We can estimate the model parameters by fitting the linear regression model
E [Y |A, V ] = θ
0
+θ
1
A+θ
2
V A+θ
3
V via weighted least squares with IP weights
W
A
or SW
A
. In most settings, the vector of covariates L should include V .
Even when V and A are independent given the other components of L and V is
not needed to ensure exchangeability, including V in L will generally increase
the efficiency with which the parameters of the marginal structural model are
estimated.
Because we are considering a model for the effect of treatment within levels
of V , we now have the choice to use either f [A] or f [A|V ] in the numera-
tor of the stabilized weights. IP weighting based on the stabilized weights
SW
A
(V ) =
f [A|V ]
f [A|L]
generally results in narrower confidence intervals around
166 IP weighting and marginal structural models
the effect estimates. Some intuition for the generally increased statistical ef-
ficiency of SW
A
(V ) is that the variance of the weights SW
A
(V ) is less than
that of the weights SW
A
. We estimate SW
A
(V ) using the same approach
as for SW
A
, except that we add the covariate V to the logistic model for the
numerator of the weights.
The particular subset V of L that an investigator chooses to include in the
marginal structural model should only reflect the investigator’s substantive in-
terest. For example, a variable V should be included in the marginal structural
model if the investigator both believes that V may be an effect modifier and
has greater substantive interest in the causal effect of treatment within levels
of the covariate V than in the entire population. In our example, we found
no strong evidence of effect modification by sex as the 95% confidence interval
around the parameter estimate
ˆ
θ
2
was (−2.2, 1.9). If the investigator chooses tocode: Program 12.6
include all variables L in the marginal structural model, the stabilized weights
SW
A
(L) equal 1 and IP weighting is unnecessary because, under conditional
exchangeability, the marginal structural model is then the (unweighted) out-
come regression model that serves to fully adjust for all confounding by L (seeIf we were interested in the inter-
action between 2 treatments A and
B (as opposed to effect modifica-
tion of treatment A by variable V ;
see Chapter 5), we would include
parameters for both A and B in
the marginal structural model, and
would estimate IP weights with the
joint probability of both treatments
in the denominator. We would
assume exchangeability, positivity,
and consistency for A and B.
Chapter 15). For this reason, in a slightly humorous vein, we refer to a marginal
structural model that conditions on all variables L needed for exchangeability
as a faux marginal structural model.
In Part I we discussed that effect modification and confounding are two
logically distinct concepts. Nonetheless, many students have difficulty under-
standing the distinction because the same statistical methods—stratification
(Chapter 4) or regression (Chapter 15)—are often used both for confounder ad-
justment and detection of effect modification. Thus, there may be some advan-
tage to teaching these concepts using marginal structural models, because then
methods for confounder adjustment (IP weighting) are distinct from methods
for detection of effect modification (adding treatment-covariate product terms
to a marginal structural model).
12.6 Censoring and missing data
When estimating the causal effect of smoking cessation A on weight gain Y ,
we restricted the analysis to the 1566 individuals with a body weight mea-
surement at the end of follow-up in 1982. There were, however, 63 additional
individuals who met our eligibility criteria but were excluded from the analysis
because their weight in 1982 was not known. Selecting only individuals with
nonmissing outcome values—that is, censoring from the analysis those with
missing values—may introduce selection bias, as discussed in Chapter 8.
Let censoring C be an indicator for measurement of body weight in 1982:
1 if body weight is unmeasured (i.e., the individual is censored), and 0 if
body weight is measured (i.e., the individual is uncensored). Our analysis
was necessarily restricted to uncensored individuals, i.e., those with C = 0,
because those were the only ones with known values of the outcome Y . That
is, in sections 12.2 and 12.4 we did not fit the (weighted) outcome regression
model E[Y |A] = θ
0
+ θ
1
A, but rather the model E[Y |A, C = 0] = θ
0
+ θ
1
A
restricted to individuals with C = 0.
Unfortunately, even under the null, selecting only uncensored individuals
for the analysis is expected to induce bias when C is either a collider on a
pathway between treatment A and the outcome Y , or the descendant of one
such collider. See the causal diagrams in Figures 8.3 to 8.6. Our data are
12.6 Censoring and missing data 167
consistent with the structure depicted by those causal diagrams: treatment A
is associated with censoring C—5.8% of quitters versus 3.2% nonquitters were
censored—and at least some predictors of Y are associated with C—the average
baseline weight was 76.6 kg in the censored versus 70.8 in the uncensored.
Because censoring due to loss to follow-up can introduce selection bias, we
are generally interested in the causal effect if nobody in the study population
had been censored. In our example, the goal becomes estimating the mean
weight gain if everybody had quit smoking and nobody’s outcome had been
censored, E[Y
a=1,c=0
], and the mean weight gain if nobody had quit smoking
and nobody’s outcome had been censored E[Y
a=0,c=0
]. Then the causal effect
of interest is E[Y
a=1,c=0
] − E[Y
a=0,c=0
], a joint effect of A and C as we dis-
cussed in Chapter 8. The use of the superscript c = 0 makes it explicit the
causal contrast that many have in mind when they refer to the causal effect of
treatment A, even if they choose not to use the superscript c = 0.
This causal effect can be estimated by using IP weights W
A,C
= W
A
×W
C
The IP weights for censoring
and treatment are W
A,C
=
1/f (A, C = 0|L), where the joint
density of A and C is factored
as f (A, C = 0|L) = f (A|L) ×
Pr [C = 0|L, A].
in which W
C
= 1/ Pr [C = 0|L, A] for the uncensored individuals and W
C
= 0
for the censored individuals. The IP weights W
A,C
adjust for both confounding
and selection bias under the identifiability conditions of exchangeability for the
joint treatment (A, C) conditional on L—that is, Y
a,c=0
⊥⊥(A, C) |L—, joint
positivity for (A = a, C = 0), and consistency. If some of the variables in L
are affected by treatment A as in Figure 8.4, the conditional independence
Y
a,c=0
⊥⊥(A, C) |L will not generally hold. In Part III we show that there are
alternative exchangeability conditions that license us to use IP weighting to
estimate the joint effect of A and C when some components of L are affected
by treatment.Some variables in L may have
zero coefficients in the model for
f (A|L) but not in the model
for Pr [C = 0|L, A], or vice versa.
Nonetheless, in large samples, it is
always more efficient to keep all
variables L that independently pre-
dict the outcome in both models.
Remember that the weights W
C
= 1/ Pr [C = 0|L, A] create a pseudo-
population with the same size as that of the original study population be-
fore censoring, and in which there is no arrow from either L or A into C.
In our example, the estimates of IP weights for censoring W
C
will create a
pseudo-population with (approximately) 1566+ 63 = 1629 in which, under our
assumptions, there is no selection bias because there is no selection. That is,
we fit the weighted model E[Y |A, C = 0] = θ
0
+ θ
1
A with weights W
A,C
to
estimate the parameters of the marginal structural model E[Y
a,c=0
] = β
0
+β
1
a
in the entire population.
Alternatively, one can use stabilized IP weights SW
A,C
= SW
A
× SW
C
.
The censoring weights SW
C
= Pr [C = 0|A] / Pr [C = 0|L, A] create a pseudo-The estimated IP weights SW
C
have mean 1 when the model for
Pr [C = 0|A] is correctly specified.
See Technical Point 12.2 for more
on stabilized IP weights.
population of the same size as the original study population after censoring,
and in which there is no arrow from L into C. In our example, the estimates
of IP weights for censoring SW
C
will create a pseudo-population of (approx-
imately) 1566 uncensored individuals. That is, the stabilized weights do not
eliminate censoring in the pseudo-population, they make censoring occur at
random with respect to the measured covariates L. Therefore, under our as-
sumption of conditional exchangeability of censored and uncensored individ-
uals given L (and A), the proportion of censored individuals in the pseudo-
population is identical to that in the study population: there is selection but
no selection bias.
To obtain parametric estimates of Pr [C = 0|L, A] in our example, we fit a
logistic regression model for the probability of being uncensored to the 1629
individuals in the study population. The model included the same covariates
we used earlier to estimate the weights for treatment. Under these paramet-
ric restrictions, we obtained an estimate
c
Pr [C = 0|L, A] and an estimate of
SW
C
for each of the 1566 uncensored individuals. Using the stabilized weights
SW
A,C
= SW
A
× SW
C
we estimated that quitting smoking increases weight
168 IP weighting and marginal structural models
Technical Point 12.2
More on stabilized weights. The stabilized weights SW
A
=
f [A]
f [A|L]
are part of the larger class of stabilized weights
g [A]
f [A|L]
, where g [A] is any function of A that is not a function of L. When unsaturated structural models are used,
weights
g [A]
f [A|L]
are preferable over weights
1
f [A|L]
because there exist functions g [A] (often f [A] is one) that can be
used to construct more efficient estimators of the causal effect in a nonsaturated marginal structural model.
Although the IP weighted mean E
g (A) I (A = a) Y
f (A|L)
with weights
g [A]
f [A|L]
is no longer equal to
the counterfactual mean E [Y
a
] under exchangeability and positivity, the Hajek version of the IP
weighted mean E
g (A) I (A = a) Y
f (A|L)
/ E
g (A) I (A = a)
f (A|L)
does equal E [Y
a
], since E
g (A) I (A = a) Y
f (A|L)
=
g (a) E
I (A = a) Y
f (A|L)
= g (a) E [Y
a
] and E
g (A) I (A = a)
f (A|L)
= g (a). The Hajek mean is the solution u
to the equation E
g [A]
f [A|L]
(Y − u)
= 0. Similarly, in the simplest marginal structural model E[Y
a
] =
β
0
+ β
1
a, the weighted least squares estimators
b
β
0
,
b
β
1
with weights
g [A]
f [A|L]
solve the estimating equations
b
E
g [A]
f [A|L]
[Y − (β
0
+ β
1
A)]
1
A
= 0. The estimates
b
β
0
of E
Y
0
and
b
β
0
+
b
β
1
of E
Y
1
are precisely the
Hajek versions of the weighted mean with the expectations replaced by sample averages. Finally, arguing as in Technical
Point 2.2, it can be shown that, in the pseudo-population created using the weights
g [A]
f [A|L]
, the mean of Y given
A = a still equals E [Y
a
].
by
ˆ
θ
1
= 3.5 kg (95% confidence interval: 2.5, 4.5) on average. This is almost thecode: Program 12.7
The estimated IP weights SW
A,C
ranged from 0.35 to 4.09, and their
mean was 1.00.
same estimate we obtained earlier using IP weights SW
A
, which suggests that
either there is no selection bias by censoring or that our measured covariates
are unable to eliminate it.
We now describe an alternative to IP weighting to adjust for confounding
and selection bias: standardization.
Chapter 13
STANDARDIZATION AND THE PARAMETRIC G-FORMULA
In this chapter we describe how to use standardization to estimate the average causal effect of smoking cessation
on body weight gain. We use the same observational data set as in the previous chapter. Though standardization
was introduced in Chapter 2, we only described it as a nonparametric method. We now describe the use of models
together with standardization, which will allow us to tackle high-dimensional problems with many covariates and
nondichotomous treatments. As in the previous chapter, we provide computer code to conduct the analyses.
In practice, investigators will often have a choice between IP weighting and standardization as the analytic
approach to obtain effect estimates from observational data. Both methods are based on the same identifiability
conditions, but on different modeling assumptions.
13.1 Standardization as an alternative to IP weighting
In the previous chapter we estimated the average causal effect of smoking ces-
sation A (1: yes, 0: no) on weight gain Y (measured in kg) using IP weighting.
In this chapter we will estimate the same effect using standardization. Our
analyses will also be based on NHEFS data from 1629 cigarette smokers aged
25-74 years who had a baseline visit and a follow-up visit about 10 years later.
Of these, 1566 individuals had their weight measured at the follow-up visit and
are therefore uncensored (C = 0).
We define E[Y
a,c=0
] as the mean weight gain that would have been observed
if all individuals had received treatment level a and if no individuals had been
censored. The average causal effect of smoking cessation can be expressed as
the difference E[Y
a=1,c=0
] − E[Y
a=0,c=0
], i.e., the difference in mean weight
that would have been observed if everybody had been treated and uncensored
compared with untreated and uncensored.
As shown in Table 12.1, quitters (A = 1) and non-quitters (A = 0) differ
with respect to the distribution of predictors of weight gain. The observed
associational difference E[Y |A = 1, C = 0] − E[Y |A = 0, C = 0] = 2.5 is
expected to differ from the causal difference E[Y
a=1,c=0
] −E[Y
a=0,c=0
]. Again
we assume that the vector of variables L is sufficient to adjust for confounding
and selection bias, and that L includes the baseline variables sex (0: male,
1: female), age (in years), race (0: white, 1: other), education (5 categories),
intensity and duration of smoking (number of cigarettes per day and years of
smoking), physical activity in daily life (3 categories), recreational exercise (3
categories), and weight (in kg).
One way to adjust for the variables L is IP weighting, which creates aAs in the previous chapter, we will
assume that the components of L
required to adjust for C are unaf-
fected by A. Otherwise, we would
need to use the more general ap-
proach described in Part III.
pseudo-population in which the distribution of the variables in L is the same
in the treated and in the untreated. Then, under the assumptions of exchange-
ability and positivity given L, we estimate E[Y
a,c=0
] by simply computing
b
E[Y |A = a, C = 0] as the average outcome in the pseudo-population. If A
were a continuous treatment (contrary to our example), we would also need a
structural model to estimate E[Y |A, C = 0] in the pseudo-population for all
170 Standardization and the parametric g-formula
Fine Point 13.1
Structural positivity. Lack of structural positivity precludes the identification of the average causal effect in the entire
population when using IP weighting. Positivity is also necessary for standardization because, when Pr [A = a|L = l] = 0
and Pr [L = l] = 0, then the conditional mean outcome E[Y |A = a, L = l] is undefined.
But the practical impact of deviations from positivity may vary greatly between IP weighted and standardized estimates
that rely on parametric models. When using standardization, one can ignore the lack of positivity if one is willing to rely
on parametric extrapolation. That is, one can fit a model for E[Y |A, L] that will smooth over the strata with structural
zeroes. This smoothing will introduce bias into the estimation, and therefore the nominal 95% confidence intervals
around the estimates will cover the true effect less than 95% of the time. Also, note the different purpose of modeling
in this setting with structural positivity: we model not because we lack enough data, but because we want to estimate
a quantity that cannot be identified even with an infinite amount of data (because of structural non-positivity). This is
an important distinction.
In general, in the presence of violations or near-violations of positivity, the standard error of the treatment effect will
be smaller for standardization than for IP weighting. This does not necessarily mean that standardization is preferred
over IP weighting; the difference in the biases may swamp the differences in standard errors.
possible values of A. IP weighting requires estimating the joint distribution of
treatment and censoring. For the dichotomous treatment smoking cessation,
we estimated Pr [A = a, C = 0|L] and computed IP probability weights with
this joint probability in the denominator.
As discussed in Chapter 2, an alternative to IP weighting is standardiza-
tion. Under exchangeability and positivity conditional on the variables in L,
the standardized mean outcome in the uncensored treated is a consistent es-Technical Point 2.3 proves that,
under conditional exchangeability,
positivity, and consistency, the
standardized mean in the treated
equals the mean if everyone had
been treated. The extension to cen-
soring is trivial: just replace A = a
by (A = a, C = 0) in the proof and
definitions.
timator of the mean outcome if everyone had been treated and had remained
uncensored E[Y
a=1,c=0
]. Analogously, the standardized mean outcome in the
uncensored untreated is a consistent estimator of the mean outcome if everyone
had been untreated and had remained uncensored E[Y
a=0,c=0
]. See Fine Point
13.1 for a discussion of the relative impact of deviations from positivity in IP
weighting and in standardization.
To compute the standardized mean outcome in the uncensored treated, we
first need to compute the mean outcomes in the uncensored treated in each
stratum l of the confounders L, i.e., the conditional means E[Y |A = 1, C =
0, L = l] in each of the strata l. In our smoking cessation example, we would
need to compute the mean weight gain Y among those who quit smoking and
remained uncensored in each of the (possibly millions of) strata defined by the
combination of values of the 9 variables in L.
The standardized mean in the uncensored treated is then the weighted
average of these conditional means using as weights the prevalence of each
value l in the study population, i.e., Pr [L = l]. That is, the conditional mean
from the stratum with the greatest number of individuals has the greatest
weight in the computation of the standardized mean. The standardized mean
in the uncensored untreated is computed analogously except that the A = 1 in
the conditioning event is replaced by A = 0.
More compactly, the standardized mean in the uncensored who receivedThe average causal effect in the
treated can be estimated by stan-
dardization as described in Techni-
cal Point 4.1. One just needs to
replace Pr[L = l] by Pr[L = l|A =
1] in the expression to the right.
treatment level a is
X
l
E[Y |A = a, C = 0, L = l] × Pr [L = l]
When, as in our example, some of the variables in L are continuous, one needs
to replace Pr [L = l] by the probability density function (pdf) f
L
[l], and the
13.2 Estimating the mean outcome via modeling 171
above sum becomes an integral.
The next two sections describe how to estimate the conditional means of
the outcome Y and the distribution of the confounders L, the two types of
quantities required to estimate the standardized mean.
13.2 Estimating the mean outcome via modeling
Ideally, we would estimate the set of conditional means E[Y |A = 1, C = 0, L =
l] nonparametrically. We would compute the average outcome among the un-
censored treated in each of the strata defined by different combination of values
of the variables L. This is precisely what we did in Section 2.3, where all the
information required for this calculation was taken from Table 2.2.
But nonparametric estimation of E[Y |A = 1, C = 0, L = l] is out of the
question when, as in our current example, we have high-dimensional data with
many confounders, some of them with multiple levels. We cannot obtain mean-
ingful nonparametric stratum-specific estimates of the mean outcome in the
treated when there are only 403 treated individuals distributed across millions
of strata. We need to resort to modeling. The same rationale applies to the con-
ditional mean outcome in the uncensored untreated E[Y |A = 0, C = 0, L = l].
To obtain parametric estimates of E[Y |A = a, C = 0, L = l] in each of the
millions of strata defined by L, we fit a linear regression model for the mean
weight gain with treatment A and all 9 confounders in L included as covariates.
We used linear and quadratic terms for the (quasi-)continuous covariates age,
weight, intensity and duration of smoking. That is, our model restricts the
possible values of E[Y |A = a, C = 0, L = l] such that the conditional relation
between the continuous covariates and the mean outcome can be represented
by a parabolic curve. We included a product term between smoking cessation
A and intensity of smoking. That is, our model imposes the restriction that
each covariate’s contribution to the mean does not depend on that of the other
covariates, except that the contribution of smoking cessation A varies linearly
with intensity of prior smoking.code: Program 13.1
Under these parametric restrictions, we obtained an estimate
b
E[Y |A =
a, C = 0, L = l] for each combination of values of A and L, and therefore
for each of the 403 uncensored treated (A = 1, C = 0) and each of the 1163
uncensored untreated (A = 0, C = 0) individuals in the study population.
For example, we estimated that individuals with the combination of values
{non-quitter, male, white, age 26, college dropout, 15 cigarettes/day, 12 years
of smoking habit, moderate exercise, very active, weight 112 kg} had a mean
weight gain of 0.34 kg (the individual with unique identifier 24770 happened toIn general, the standardized mean
of Y is written as
R
E [Y |A = a, C = 0, L = l] dF
L
(l)
where F
L
(·) is the joint cumulative
distribution function (cdf) of the
random variables in L. When, as in
this chapter, L is a vector of base-
line covariates unaffected by treat-
ment, we can average over the ob-
served values of L to nonparamet-
rically estimate this integral.
have these combination of values, you may take a look at his predicted value).
Overall, the mean of the estimated weight gain was 2.6 kg, same as the mean of
the observed weight gain, which ranged from −41.3 to 48.5 kg across different
combinations of covariates.
Remember that our goal is to estimate the standardized mean
P
l
E[Y |A =
a, C = 0, L = l]×Pr [L = l] in the treated (A = 1) and in the untreated (A = 0).
More formally, the standardized mean should be written as an integral because
some of the variables in L are essentially continuous, and thus their distribution
cannot be represented by a probability function. Regardless of these notational
issues, we have already estimated the means E[Y |A = a, C = 0, L = l] for all
values of treatment A and confounders L.
172 Standardization and the parametric g-formula
The next step is standardizing these means to the distribution of the con-
founders L for all values l.
13.3 Standardizing the mean outcome to the confounder distribution
The standardized mean is a weighted average of the conditional means E[Y |A =
a, C = 0, L = l]. When all variables in L are discrete, each mean receives aSecond block: All untreated
L A Y
Rheia 0 0 .
Kronos 0 0 .
Demeter 0 0 .
Hades 0 0 .
Hestia 0 0 .
Poseidon 0 0 .
Hera 0 0 .
Zeus 0 0 .
Artemis 1 0 .
Apollo 1 0 .
Leto 1 0 .
Ares 1 0 .
Athena 1 0 .
Hephaestus 1 0 .
Aphrodite 1 0 .
Polyphemus 1 0 .
Persephone 1 0 .
Hermes 1 0 .
Hebe 1 0 .
Dionysus 1 0 .
Third block: All treated
L A Y
Rheia 0 1 .
Kronos 0 1 .
Demeter 0 1 .
Hades 0 1 .
Hestia 0 1 .
Poseidon 0 1 .
Hera 0 1 .
Zeus 0 1 .
Artemis 1 1 .
Apollo 1 1 .
Leto 1 1 .
Ares 1 1 .
Athena 1 1 .
Hephaestus 1 1 .
Aphrodite 1 1 .
Polyphemus 1 1 .
Persephone 1 1 .
Hermes 1 1 .
Hebe 1 1 .
Dionysus 1 1 .
weight equal to the proportion of individuals with values L = l, i.e., Pr [L = l].
In principle, these proportions Pr [L = l] could be calculated nonparametri-
cally from the data: we would divide the number of individuals in the strata
defined by L = l by the total number of individuals in the population. This is
precisely what we did in Section 2.3, where all the information required for this
calculation was taken from Table 2.2. However, this method becomes tedious
for high-dimensional data with many confounders, some of them with multiple
levels, as in our smoking cessation example.
Fortunately, we do not need to estimate Pr [L = l]. We only need to es-
timate E [Y |A = a, C = 0, L = l] for the l value of each individual i in the
study, and then compute the average
1
n
n
P
i=1
b
E [Y |A = a, C = 0, L
i
] where n is
the number of individuals in the study. This is so because the weighted mean
P
l
E [Y |A = a, C = 0, L = l] Pr [L = l] can also be written as the double ex-
pectation E [E [Y |A = a, C = 0, L]].
We now describe a simple computational method to estimate the standard-
ized means
P
l
E[Y |A = a, C = 0, L = l]×Pr [L = l] in the treated (A = 1) and
in the untreated (A = 0) with many confounders, without ever explicitly esti-
mating Pr [L = l]. We first apply the method to the data in Table 2.2, in which
there was no censoring, the confounder L is only one variable with two levels,
and Y is a dichotomous outcome, i.e., the mean E[Y |A = a, C = 0, L = l] is the
risk Pr[Y = 1|A = a, L = l] of developing the outcome. Then we apply it to
the real data with censoring and many confounders. The method has 4 steps:
expansion of dataset, outcome modeling, prediction, and standardization by
averaging.
Table 2.2 has 20 rows, one per individual in the study. We now create a
new dataset in which the data of Table 2.2 is copied three times. That is, the
analytic dataset has 60 rows in three blocks of 20 individuals each. We leave
the first block of 20 rows as is, i.e., the first block is identical to the data in
Table 2.2. We modify the data of the second and third blocks as shown in the
margin. In the second block, we set the value of A to 0 (untreated) for all
20 individuals; in the third block we set the value of A to 1 (treated) for all
individuals. In the second and third blocks, we delete the data on the outcome
for all individuals, i.e., the variable Y is assigned a missing value. As described
below, we will use the second block to estimate the standardized mean in the
untreated and the third block for the standardized mean in the treated.
Next we use the 3-block dataset to fit a regression model for the mean
outcome given treatment A and the confounder L. We add a product term
A × L to make the model saturated. Note that only the rows in the first
block of the dataset (the actual data) will contribute to the estimation of the
parameters of the model because the outcome is missing for all rows in the
second and third blocks.
The next step is to use the parameter estimates from the first block to
13.4 IP weighting or standardization? 173
predict the outcome values for all rows in the second and third blocks. (That
is, we combine the values of the columns L and A with the regression estimates
to impute the missing value for the outcome Y .) The predicted outcome values
for the second block are the mean estimates for each combination of values of L
and A = 0, and the predicted values for the third block are the mean estimates
for each combinations of values of L and A = 1.
Finally, we compute the average of all predicted values in the second block.
Because 60% of rows have value L = 1 and 40% have value L = 0, this average
gives more weight to rows with L = 1. That is, the average of all predicted
values in the second block is precisely the standardized mean outcome in the
untreated. We are done. To estimate the standardized mean outcome in the
treated, we compute the average of all predicted values in the third block.
The above procedure yields exactly the same estimates of the standardizedcode: Program 13.2
means (0.5 for both of them) as the direct calculation in Section 2.3. Both
approaches are completely nonparametric. In this chapter we did not directly
estimate the distribution of L, but rather average over the observed values of
L, i.e., its empirical distribution.
The use of the empirical distribution for standardizing is the way to go in
more realistic examples, like our smoking cessation study, with high-dimensional
L. The procedure for our study is analogous to the one described above for
the data in Table 2.2. We add the second and third blocks to the dataset, fit
the regression model for E[Y |A = a, C = 0, L = l] as described in the previous
section, and generate the predicted values. The average predicted value in thecode: Program 13.3
second block—the standardized mean in the untreated—was 1.66, and the aver-
age predicted value in the third block—the standardized mean in the treated—
was 5.18. Therefore, our estimate of the causal effect E[Y
a=1,c=0
]−E[Y
a=0,c=0
]
was 5.18 −1.66 = 3.5 kg. To obtain a 95% confidence interval for this estimatecode: Program 13.4
we used a statistical technique known as bootstrapping (see Technical Point
13.1). In summary, we estimated that quitting smoking increases body weight
by 3.5 kg (95% confidence interval: 2.6, 4.5).
13.4 IP weighting or standardization?
We have now described two ways in which modeling can be used to estimate
the average causal effect of a treatment: IP weighting (previous chapter) and
standardization (this chapter). In our smoking cessation example, both yielded
almost exactly the same effect estimate. Indeed Technical Point 2.3 proved that
the standardized mean equals the IP weighted mean.
Why are we then bothering to estimate the standardized mean in this chap-
ter if we had already estimated the IP weighted mean in the previous chapter?
It turns out that the IP weighted and the standardized mean are only ex-
actly equal when no models are used to estimate them. Otherwise they are
expected to differ. To see this, consider the quantities that need to be mod-
eled to implement either IP weighting or standardization. IP weighting mod-
els Pr [A = a, C = 0|L], which we estimated in the previous chapter by fitting
parametric logistic regression models for Pr [A = a|L] and Pr [C = 0|A = a, L].
Standardization models the conditional means E[Y |A = a, C = 0, L = l], which
we estimated in this chapter using a parametric linear regression model.
In practice some degree of misspecification is inescapable in all models, and
model misspecification will introduce some bias. But the misspecification of
the treatment model (IP weighting) and the outcome model (standardization)
174 Standardization and the parametric g-formula
Technical Point 13.1
Bootstrapping. In Chapter 10, we discussed the foundations of random variability for causal effects. Effect estimates
need to be presented with measures of variability such as the standard error (or functions of the standard error like
the 95% confidence interval). Because of the computational difficulty to obtain exact estimates, in practice standard
error estimates are often based on large-sample approximations, which rely on asymptotic considerations. However,
sometimes even large-sample approximations are too complicated to be calculated.
The bootstrap is an alternative method for estimating standard errors and computing 95% confidence intervals. We
sketch below the simplest version, the nonparametric bootstrap, which we used to compute the 95% confidence interval
around the effect estimate of smoking cessation.
Take the study population of 1629 individuals. Sample with replacement 1629 individuals from the study population,
so that some of the original individuals may appear more than once while others may not be included at all. This new
sample of size 1629 is referred to as a “bootstrap sample.” Compute the effect of interest in the bootstrap sample (e.g.,
by using standardization as described in the main text). Now create a second bootstrap sample by again sampling with
replacement 1629 individuals. Compute the effect of interest in the second bootstrap sample using the same method
as for the first bootstrap sample. By chance, the first and second bootstrap sample will generally include a different
number of copies of each individual, and therefore will result in different effect estimates. Repeat the procedure in a
large number (say, 1000) of bootstrap samples. It turns out that the standard deviation of the 1000 effect estimates
in the bootstrap samples consistently estimates the standard error of the effect estimate in the study population. The
95% confidence interval is then computed by using the usual normal approximation: ±1.96 times the estimate of the
standard error. See, e.g., Wasserman (2004) for an introduction to the statistical theory underlying the bootstrap.
We used this bootstrap method with 1000 bootstrap samples to obtain the 95% confidence interval described in
the main text for the standardized mean difference. The bootstrap is a general method for large samples: Generally,
when the limiting distribution of an estimator is normal, 95% Wald confidence intervals centered on the estimator
with standard errors estimated by the nonparametric bootstrap will be calibrated in large samples. Thus, a 95% Wald
confidence interval for the IP weighted estimates from marginal structural models will be calibrated if standard errors
are estimated by the bootstrap, but it will often be conservative and wider if estimated by the (square root of) the
robust variance estimator described earlier.
Though the nonparametric bootstrap is a simple method, it can be computationally intensive for very large datasets.
It is therefore common to see published estimates that are based on only 200-500 bootstrap samples. While this reduction
in samples would have resulted in an almost identical confidence interval in our example, that may not be always the
case. A better way to overcome these computational challenges, while preserving the advantages of bootstrapping, is
the clever approach known as “bag of little bootstraps”(Kleiner et al. 2014).
will not generally result in the same magnitude and direction of bias in the ef-
fect estimate. Therefore the IP weighted estimate will generally differ from the
standardized estimate because unavoidable model misspecification will affect
the point estimates differently. Large differences between the IP weighted and
standardized estimate will alert us to the presence of serious model misspec-
ification in at least one of the estimates. Small differences do not guarantee
absence of serious model misspecification, but will be reassuring—though log-
ically possible, it is unlikely that badly misspecified models resulting in bias of
similar magnitude and direction for both methods.
In our smoking cessation example, both the IP weighted and the standard-
ized estimates are similar. After rounding to one decimal place, the estimated
weight gain due to smoking cessation was 3.5 kg regardless of whether we fit a
model for treatment A (IP weighting) or for the outcome Y (standardization).
In neither case did we fit a model for the confounders L, as we did not need
the distribution of the confounders to obtain the IP weighted estimate and we
were able to use the empirical distribution of L (a nonparametric method) to
13.5 How seriously do we take our estimates? 175
compute the standardized estimate.
Both IP weighting and standardization are estimators of the g-formula, a
general method for causal inference first described in 1986. (Part III provides
a definition of the g-formula in settings with time-varying treatments.) We say
that standardization is a plug-in g-formula estimator because it simply replaces
the conditional mean outcome in the g-formula by its estimates. When, like
in this chapter, those estimates come from parametric models, we refer to the
method as the parametric g-formula. Because here we were only interested in
the average causal effect, we estimated parametrically the conditional mean
outcome.
More generally, the parametric g-formula for the probability density func-
tion or pdf) requires estimates of the conditional distribution of the outcome
within levels of A and L to compute its standardized value. In the absenceRobins (1986) described the gen-
eralization of standardization to
time-varying treatments and con-
founders, and named it the g-
computation algorithm formula.
Because this name is very long,
some authors have abbreviated it
to g-formula and other authors to
g-computation. Even though g-
formula and g-computation are syn-
onyms, this book uses only the
former term because the latter
term is frequently confused with g-
estimation, a different method de-
scribed in Chapter 14.
of time-varying confounders (see Part III), the parametric g-formula does not
require parametric modeling of the distribution of the confounders.
Often there is no need to choose between IP weighting and the parametric
g-formula. When both methods can be used to estimate a causal effect, just
use both methods. Also, whenever possible, use doubly robust methods that
combine models for treatment and for outcome in the same estimator. Under
exchangeability and positivity given L, a doubly robust estimator consistently
estimates the average causal effect if either the model for the treatment or the
model for the outcome is correct, without knowing which of the two models is
the correct one. A particular doubly robust estimator, the doubly robust plug-
in estimator is discussed in Fine Point 13.2. A second doubly robust estimator,
the augmented IP weighted estimator, is discussed in Technical Point 13.2. The
mathematical relationship between the two is discussed in Technical Point 13.3.
Finally, note that we used the parametric g-formula to estimate the average
causal effect in the entire population of interest. Had we been interested in
the average causal effect in a particular subset of the population, we could
have restricted our calculations to that subset. For example, if we had been
interested in potential effect modification by sex, we would have estimated the
standardized means in men and women separately. Both IP weighting and the
parametric g-formula can be used to estimate average causal effects in either
the entire population or a subset of it.
13.5 How seriously do we take our estimates?
We spent Part I of this book reviewing the definition of average causal ef-
fect, the assumptions required to estimate it, and many potential biases. The
discussion was purely conceptual, the data examples hypersimplistic. A key
message was that a causal analysis of observational data is sharper when ex-
plicitly emulating a (hypothetical) randomized experiment—the target trial.
The analyses in this and the previous chapter are our first attempts at
estimating causal effects from real data. Using both IP weighting and the
parametric g-formula we estimated that the mean weight gain would have
been 5.2 kg if everybody had quit smoking compared with 1.7 kg if nobody
had quit smoking. Both methods estimated that quitting smoking increases
weight by 3.5 kg (95% confidence interval: 2.5, 4.5) on average in this particular
population. In the next chapters we will see that similar estimates are obtained
when using g-estimation, outcome regression, and propensity scores.
The compatibility of estimates across methods is reassuring because each
176 Standardization and the parametric g-formula
Fine Point 13.2
A doubly robust plug-in estimator. The previous chapter describes IP weighting, a method that requires a correct
model for treatment A conditional on the confounders L. This chapter describes standardization, a method that requires
a correct model for the outcome Y conditional on treatment A and the confounders L. How about a method that
requires a correct model for either treatment A or outcome Y ? That is precisely what doubly robust estimation does.
Under the usual identifiability assumptions, a doubly robust estimator consistently estimates the causal effect if at least
one of the two models is correct (and one need not know which of the two models is correct). That is, doubly robust
estimators give us two chances to get it right.
There are many types of doubly robust estimators. Here we describe a doubly robust estimator (Bang and Robins,
2005) for the average causal effect of a dichotomous treatment A on an outcome Y . For simplicity, we consider a
setting without censoring.
To obtain a doubly robust estimate of the average causal effect, first estimate the IP weight W
A
= 1/f (A|L) as
described in the previous chapter. Then fit an outcome regression model like the one described in this chapter—a
generalized linear model with a canonical link—for E[Y |A, L, R] that adds the covariate R, where R = W
A
if A = 1
and R = −W
A
if A = 0. Finally, use the predicted values with A set to 1 for every individual from the outcome model
to obtain an estimate of the standardized mean outcomes under A = 1, and repeat but with A = 0 set to 0 to obtain
an estimate of the standardized mean outcome under A = 0. Then the difference of the two estimators is a doubly
robust plug-in estimator of the average causal effect.
method’s estimate is based on different modeling assumptions. However, ob-
servational effect estimates are always open to serious criticism. Even if we
do not wish to transport our effect estimate to other populations (Chapter 4)
and even if there is no interference between individuals, the validity of our es-
timates for the target population requires many conditions. We classify these
conditions in three groups.
First, the identifiability conditions of exchangeability, positivity, and con-
sistency (Chapter 3) need to hold for the observational study to resemble the
target trial. The quitters and the non-quitters need to be exchangeable con-
ditional on the 9 measured covariates L (see Fine Point 14.2). Unmeasured
confounding (Chapter 7) or selection bias (Chapter 8, Fine Point 12.2) would
prevent conditional exchangeability. Positivity requires that the distributionMethods based on outcome regres-
sion (including doubly robust meth-
ods) can be used in the absence
of positivity, under the assumption
that the outcome model is correctly
specified to extrapolate beyond the
data. See Fine Point 13.1.
of the covariates L in the quitters fully overlaps with that in the non-quitters.
Fine Point 13.1 discussed the different impact of deviations from positivity
for nonparametric IP weighting and standardization. Regarding consistency,
note that there are multiple versions of both quitting smoking (e.g., quitting
progressively, quitting abruptly) and not quitting smoking (e.g., increasing in-
tensity of smoking by 2 cigarettes per day, reducing intensity but not to zero).
Our effect estimate corresponds to a somewhat vague hypothetical interven-
tion in the target population that randomly assigns these versions of treatment
with the same frequency as they actually have in the study population. OtherThis dependence of the numerical
estimate on the exact interventions
is important when the estimates are
used to guide decision making in
public policy or clinical medicine
(Hern´an 2016).
hypothetical interventions might result in a different effect estimate.
Second, all variables used in the analysis need to be correctly measured.
Measurement error in the treatment A, the outcome Y , or the confounders L
will generally result in bias (Chapter 9). In practice, some degree of mismea-
surement of most variables is unavoidable.
Third, all models used in the analysis need to be correctly specified (Chap-
ter 11). Suppose that the correct functional form for the continuous covariate
age in the treatment model is not the parabolic curve we used but rather a
curve represented by a complex polynomial. Then, even if all the confounders
13.5 How seriously do we take our estimates? 177
had been correctly measured and included in L, IP weighting would not fully
adjust for confounding. Model misspecification has a similar effect as measure-
ment error in the confounders.
Ensuring that each of these conditions hold, at least approximately, is the
investigator’s most important task. If these conditions could be guaranteed
to hold, then the data analysis would be trivial. The problem is, of course,
that one cannot ever expect that any of these conditions will hold perfectly.
Unmeasured confounders, nonoverlapping confounder distributions, ill-defined
interventions, mismeasured variables, and misspecified models will typically
lurk behind our estimates. Some of these problems may be addressed em-The validity of our causal inferences
requires the following conditions
• exchangeability
• positivity
• consistency
• no measurement error
• no model misspecification
pirically, but others will remain a matter of subject-matter judgement, and
therefore open to criticism that cannot be refuted by our data. For example,
we can propose different model specifications but we cannot adjust for variables
that were not measured.
The effect estimates reported above are only unbiased for the average causal
effect of smoking cessation if all of these (heroic) conditions hold. The more
our study deviates from those conditions, the more biased our effect estimate
may be. These conditions are not empirically testable because we lack of data
on the distribution of the counterfactual outcomes. Therefore, in practice, we
make the assumption that the above conditions are approximately met. Our
assumption needs to be supported by expert knowledge, as we discussed in
Section 7.6 for lack of exchangeability due to confounding.
Expert knowledge, however, is incomplete. As a result, existing expert
knowledge is typically compatible with a range of conditions from essentially
perfect exchangeability because all known confounders are unmeasured to mod-
erate lack of exchangeability because perhaps we do not know about some con-
founders. Therefore, in practice, we need to conduct analyses under different
assumptions to explore the sensitivity of our effect estimates to our original
assumptions. In this book, we refer to sensitivity analysis for confounding (see
citations in Fine Point 7.1) via negative outcome controls (Technical Point
7.5) and g-estimation (Fine Point 14.2), for selection bias (Fine Point 12.1),
and for model misspecification (Section 11.5). The sensitivity of the effect
estimates to our reliance on unverifiable conditions can also be explored via
quantitative bias analysis (Fine Point 10.2) or, sometimes, by using alternative
unverifiable conditions such as those required for instrumental variable estima-In the presence of unmeasured con-
founders, alternative sets of iden-
tifiability conditions are proximal
causal inference (Technical Point
7.3) and the front door criterion
(Technical Point 7.4).
tion (see Chapter 16). Ideally, sensitivity analyses would be incorporated in
all causal inference research projects.
A healthy skepticism of causal inferences drawn from observational data is
necessary. To be productive, this skepticism needs to be grounded on expert
knowledge about the validity of our assumptions. A key step towards less casual
causal inferences is the realization that the discussion should primarily revolve
around each of the above assumptions. We only take our effect estimates as
seriously as we take the conditions that are needed to endow them with a
causal interpretation.
178 Standardization and the parametric g-formula
Technical Point 13.2
Augmented IP weighted estimator. Suppose we have a dichotomous treatment A, an outcome Y , and a vector of
measured variables L that satisfy positivity and exchangeability (consistency is assumed). For simplicity, we consider
estimation of the counterfactual mean outcome under treatment E[Y
a=1
] rather than the causal effect. Then E[Y
a=1
]
can be written as either E[b(L)], where b(L) = E[Y |A = 1, L], or E[
AY
π(L)
], where π(L) = Pr [A = 1|L]. In this chapter,
we described a plug-in g-formula estimator
1
n
n
P
i=1
ˆ
b(L
i
) that replaces the conditional mean outcome by its estimate from
a (say, linear) parametric regression model for b(L) and averages it over all n individuals in the study. In the previous
chapter, we described a Horvitz-Thompson IP weighted estimator
1
n
n
P
i=1
A
i
Y
i
ˆπ(L
i
)
that replaces the probability of treatment
by its estimate from a (say, logistic) parametric regression model for π(L) and averages it over the n individuals. The
bias of the plug-in g-formula estimator will be large if the estimate
ˆ
b(L) is far from b(L), and the bias of the IP weighted
estimator will be large if ˆπ(L) is far from π(L).
A doubly robust estimator of E[Y
a=1
] appropriately combines the estimate
ˆ
b(L) from the outcome model and the
estimate ˆπ(L) from the treatment model. There are many forms of doubly robust estimators, like the one described
in Fine Point 13.2 for the average causal effect. All doubly robust estimators involve a correction of the outcome
regression model by a function that involves the treatment model, which can also be viewed as a correction of the
Horvitz-Thompson estimator by a function that involves the outcome regression model. For example, consider the
following doubly robust estimator of E[Y
a=1
]:
b
E[Y
a=1
]
DR
=
1
n
n
X
i=1
ˆ
b(L
i
) +
A
i
ˆπ(L
i
)
Y
i
−
ˆ
b(L
i
)
,
which can also be written as
1
n
n
P
i=1
h
A
i
Y
i
ˆπ(L
i
)
−
A
i
ˆπ(L
i
)
− 1
ˆ
b(L
i
)
i
. Motivated by the latter formula
b
E[Y
a=1
]
DR
is referred
to as the augmented IP weighted estimator.
Under exchangeability and positivity, the bias of this doubly robust estimator of E[Y
a=1
] is small if either the estimate
ˆ
b(L) is close to b(L) or the estimate ˆπ(L) is close to π(L). Specifically, the difference
b
E[Y
a=1
]
DR
−E[Y
a=1
] will converge
in probability to
E
π(L)
1
π(L)
−
1
π
∗
(L)
(b(L) − b
∗
(L))
,
where π
∗
(l) and b
∗
(l) are the probability limits of ˆπ(l) and
ˆ
b(l). It follows that our doubly robust estimator is (asymp-
totically) unbiased when either the parametric outcome model is correct [so b
∗
(l) = b(l)] or the parametric treatment
model is correct [so π
∗
(l) = π(l)]. Furthermore, we do not need to know which one of the two models is correct. Of
course, one does not expect any parametric model to be correctly specified if the vector L is very high-dimensional and
thus even the bias of our doubly robust estimator may be large.
However, all doubly robust estimators have the property that the bias depends on the product of the error
1
π(l)
−
1
ˆπ(l)
in the estimation of
1
π(l)
with the error b(l) −
ˆ
b(l) in the estimation of b(l). As we discuss in Chapter 18, this property—
which is known as second-order bias—allows us to construct doubly-robust estimators of E[Y
a=1
] that may have small
bias by estimating π(l) and b(l) with machine learning estimators rather than with standard parametric models. This is
because, in high-dimensional settings in which large amounts of data are available, machine learning estimators based
on complex algorithms, produce more accurate estimators of π(l) and b(l) than standard parametric models.
13.5 How seriously do we take our estimates? 179
Technical Point 13.3
The relationship between the augmented IP weighted estimator and the doubly robust plug-in estimator.
Consider again the counterfactual mean outcome E[Y
a
] ≡ ψ
a
and assume the identifiability conditions hold. Then,
ψ
a
= E[b(a, L)], where b(a, L) = E[Y |A = a, L]; also, ψ
a
= E [I (A = a) Y/f (a|L)]. As discussed in Technical Point
13.2, the augmented IP weighted (AIPW) estimator
b
ψ
a,AIP W
of the counterfactual mean outcome E[Y
a
] ≡ ψ
a
is
P
n
"
I (A = a) Y
b
f (A|L)
−
I (A = a)
b
f (A|L)
− 1
!
b
b (a, L)
#
= P
n
h
b
b (a, L) + I (A = a)
n
Y −
b
b (A, L)
o
/
b
f (A|L)
i
where P
n
[H] ≡
1
n
n
P
i=1
H
i
for any H, and
b
f (a|L) and
b
b (a, L) are estimators of f (a|L) and b (a, L), respectively
(Robins et al. 1994, Robins and Ritov 1997). The estimator is doubly robust because (i) if
b
f (a|L) is consistent then
the left-hand side of the above equality converges in probability to ψ
a
= E [I (A = a) Y /f (a|L)] and (ii) if
b
b (a, L)
is consistent, the right-hand side of the equality converges to ψ
a
= E[b(a, L)]. It follows that the AIPW estimator
b
ψ
1,AIP W
−
b
ψ
0,AIP W
of the average causal effect E[Y
1
] −E
Y
0
= ψ
1
−ψ
0
is doubly robust as it is consistent if either
(i)
b
f (a = 1|L) = 1 −
b
f (a = 0|L) is consistent or (ii) both
b
b (1, L) and
b
b (0, L) are consistent.
Now that we have a doubly robust AIPW estimator, how do we obtain the doubly robust plug-in estimator of Fine Point
13.2? From the right-hand side of the above equality, we have
b
ψ
1,AIP W
−
b
ψ
0,AIP W
= P
n
h
b
b (1, L)
i
− P
n
h
b
b (0, L)
i
−
P
n
{
Y −
b
b(A,L)
}
b
f(A|L)
{I (A = 1) − I (A = 0)}
. If we want a doubly robust plug-in estimator P
n
h
b
b (1, L)
i
− P
n
h
b
b (0, L)
i
,
we require that, in every sample,
P
n
"
Y −
b
b (A, L)
b
f (A|L)
{I (A = 1) − I (A = 0)}
#
= 0
This above equation will hold if
b
b (A, L) = b
A, L;
b
β,
b
θ
is the iteratively reweighted least squares (IRLS) estimate of the
model E[Y |A, L] = b (A, L; β, θ) = ϕ
h
m (A, L; β) + θ
n
{I(A=1)−I(A=0)}
b
f(A|L)
oi
, where ϕ is the inverse of a canonical link
function such as the log, logit, or linear link. This follows because the equation above is the score equation corresponding
to the parameter θ (Robins 1999, Bang and Robins 2005, Scharfstein et al. 1999). The resulting plug-in estimator is
precisely the estimator of Fine Point 13.2. The estimator is a targeted minimum loss-based estimator (TMLE), also
known as a targeted maximum likelihood estimator, and
{I(A=1)−I(A=0)}
b
f(A|L)
=
A
bπ(|L)
−
(1−A)
(1−bπ(|L))
is the “clever covariate”
in the nomenclature later introduced by van der Laan and Rubin (2006).
There exists more than one choice of model that will insure the above displayed equation holds. For example, one
could use the model for E[Y |A, L] that replaces the θ term in above model by the sum θ
1
A
bπ(|L)
+ θ
2
(1−A)
(1−bπ(|L))
and
estimate both θ
1
and θ
2
(Scharfstein et al 1999, Bang and Robins 2005). This latter estimator is also a TMLE but now
with 2 clever covariates
A
bπ(|L)
and
(1−A)
(1−bπ(|L))
. An advantage of the 2-clever covariate model over the 1-clever covariate
model is that P
n
h
b
b (1, L)
i
and P
n
h
b
b (0, L)
i
are now also doubly robust plugin estimators of E[Y
a=1
] and E[Y
a=0
]
while P
n
h
b
b (1, L)
i
− P
n
h
b
b (0, L)
i
remains a doubly robust estimator of the average treatment effect.
180 Standardization and the parametric g-formula
Chapter 14
G-ESTIMATION OF STRUCTURAL NESTED MODELS
In the previous two chapters, we described IP weighting and standardization to estimate the average causal effect
of smoking cessation on body weight gain. In this chapter we describe a third method to estimate the average
causal effect: g-estimation. We use the same observational NHEFS data and provide simple computer code to
conduct the analyses.
IP weighting, standardization, and g-estimation are often collectively referred to as g-methods because they
are designed for application to generalized treatment contrasts involving treatments that vary over time. The
application of g-methods to treatments that do not vary over time in Part II of this book may then be overkill
since there are alternative, simpler approaches. However, by presenting g-methods in a relatively simple setting,
we can focus on their main features while avoiding the more complex issues described in Part III.
IP weighting and standardization were introduced in Part I (Chapter 2) and then described with models in Part
II (Chapters 12 and 13, respectively). In contrast, we have waited until Part II to describe g-estimation. There is
a reason for that: describing g-estimation is facilitated by the specification of a structural model, even if the model
is saturated. Models whose parameters are estimated via g-estimation are known as structural nested models. The
three g-methods are based on different modeling assumptions.
14.1 The causal question revisited
In the last two chapters we have applied IP weighting and standardization to
estimate the average causal effect of smoking cessation (the treatment) A on
weight gain (the outcome) Y . To do so, we used data from 1566 cigaretteAs in previous chapters, we re-
stricted the analysis to NHEFS indi-
viduals with known sex, age, race,
weight, height, education, alcohol
use and intensity of smoking at
the baseline (1971-75) and follow-
up (1982) visits, and who answered
the medical history questionnaire at
baseline.
smokers aged 25-74 years who were classified as treated A = 1 if they quit
smoking, and as untreated A = 0 otherwise. We assumed that exchangeability
of the treated and the untreated was achieved conditional on the L variables:
sex, age, race, education, intensity and duration of smoking, physical activity
in daily life, recreational exercise, and weight. We defined the average causal
effect on the difference scale as E[Y
a=1,c=0
] − E[Y
a=0,c=0
], i.e., the difference
in mean weight that would have been observed if everybody had been treated
and uncensored compared with untreated and uncensored.
The quantity E[Y
a=1,c=0
] −E[Y
a=0,c=0
] measures the average causal effect
in the entire population. But sometimes one can be interested in the average
causal effect in a subset of the population. For example, one may want to
estimate the average causal effect in individuals aged 45—E[Y
a=1,c=0
|age =
45] − E[Y
a=0,c=0
|age = 45]—, in women, in those with low educational level,
etc. To estimate the effect in a subset of the population one can use marginal
structural models with product terms (see Chapter 12) or apply standardiza-
tion to that subset only (Chapter 13).
Suppose that the investigator is interested in estimating the causal effect of
smoking cessation A on weight gain Y in each of the strata defined by combina-
tions of values of the variables L. In our example, there are many such strata.
One of them is the stratum {non-quitter, female, white, age 26, college dropout,
15 cigarettes/day, 12 years of smoking habit, moderate exercise, very active,
182 G-estimation of structural nested models
weight 112 kg}. As described in Chapter 4, investigators with extremely large
datasets could partition the study population into mutually exclusive subsets
or non-overlapping strata, each of them defined by a particular combination
of values l of the variables in L, and then estimate the average causal effect in
each of the strata. In Section 12.5 we explain that an alternative approach is
to add all variables L, together with product terms between each component
of L and treatment A, to the marginal structural model. Then the stabilized
weights SW
A
(L) equal 1 and no IP weighting is necessary because the (un-
weighted) outcome regression model, if correctly specified, fully adjusts for all
confounding by L (see Chapter 15).
In this chapter we will use g-estimation to estimate the average causal effect
of smoking cessation A on weight gain Y in each strata defined by the covari-
ates L. This conditional effect is represented by E[Y
a=1,c=0
|L]−E[Y
a=0,c=0
|L].
Before describing g-estimation, we will present structural nested models and
rank preservation, and, in the next section, articulate the condition of ex-
changeability given L in a new way.
14.2 Exchangeability revisited
As a reminder (see Chapter 2), in our example, conditional exchangeability im-
plies that, in any subset of the study population in which all individuals haveYou may find the first paragraph
of this section repetitious and un-
necessary given our previous discus-
sions of conditional exchangeability.
If that is the case, we could not be
happier.
the same values of L, those who did not quit smoking (A = 0) would have had
the same mean weight gain as those who did quit smoking (A = 1) if they had
not quit, and vice versa. In other words, conditional exchangeability means
that the outcome distribution in the treated and the untreated would be the
same if both groups had received the same treatment level. When the distri-
bution of the outcomes Y
a
under treatment level a is the same for the treated
and the untreated, each of the counterfactual outcomes Y
a
is independent of
the actual treatment level A, within levels of the covariates, or Y
a
⊥⊥A|L for
both a = 1 and a = 0.
Take the counterfactual outcome under no treatment Y
a=0
. When condi-
tional exchangeability holds, knowing the value of Y
a=0
does not help differ-
entiate between quitters and nonquitters with a particular value of L. That is,
the conditional (on L) probability of being a quitter is the same for all values
of the counterfactual outcome Y
a=0
. Mathematically, we write
Pr[A = 1|Y
a=0
, L] = Pr[A = 1|L]
which is an equivalent definition of conditional exchangeability for a dichoto-
mous treatment A.
Expressing conditional exchangeability in terms of the conditional proba-
bility of treatment will be helpful when we describe g-estimation later in this
chapter. Specifically, suppose we propose the following parametric logistic
model for the probability of treatmentFor simplicity, in this book we do
not distinguish between vector and
scalar parameters when we believe
it does not create any confusion.
logit Pr[A = 1|Y
a=0
, L] = α
0
+ α
1
Y
a=0
+ α
2
L
where α
2
is a vector of parameters, one for each component of L. If L has p
components L
1
, ...L
p
then α
2
L =
P
p
j=1
α
2j
L
j
. This model is the same one we
used to estimate the denominator of the IP weights in Chapter 12, except that
this model also includes the counterfactual outcome Y
a=0
as a covariate.
14.3 Structural nested mean models 183
Of course, we can never fit this model to a real data set because we do
not know the value of the variable Y
a=0
for all individuals. But suppose for
a second that we had data on Y
a=0
for all individuals, and that we fit the
above logistic model. If there is conditional exchangeability and the model
is correctly specified, what estimate would you expect for the parameter α
1
?
Pause and think about it before going on (the response can be found near the
end of this paragraph) because we will be estimating the parameter α
1
when
implementing g-estimation. If you have already guessed what its value should
be, you have already understood half of g-estimation. Yes, the expected value
of the estimate of α
1
is zero because Y
a=0
does not predict A conditional on
L. We now introduce the other half of g-estimation: the structural model.
14.3 Structural nested mean models
We are interested in estimating the average causal effect of treatment A within
levels of L, i.e., E[Y
a=1
|L] − E[Y
a=0
|L]. (For simplicity, suppose there is no
censoring until later in this section.) We can also represent this effect by
E[Y
a=1
− Y
a=0
|L] because the difference of the means is equal to the mean
of the differences. If there were no effect-measure modification by L, these
differences would be constant across strata, i.e., E[Y
a=1
−Y
a=0
|L] = β
1
where
β
1
would be the average causal effect in each stratum and also in the entire
population. Our structural model for the conditional causal effect would be
E[Y
a
− Y
a=0
|L] = β
1
a. Unlike a model for the conditional means E[Y
a
|L], a
model for the mean differences E[Y
a
−Y
a=0
|L] includes neither an intercept β
0
nor a term β
2
L because both terms cancel out when computing the difference.
More generally, there may be effect modification by L. For example, the
causal effect of smoking cessation may be greater among heavy smokers than
among light smokers. To allow for the causal effect to depend on L we can add a
product term to the structural model, i.e., E[Y
a
−Y
a=0
|L] = β
1
a+β
2
aL, where
β
2
is a vector of parameters. Under conditional exchangeability Y
a
⊥⊥A|L, the
conditional effect will be the same in the treated and in the untreated because
the treated and the untreated are, on average, the same type of people within
levels of L. Thus, under exchangeability, the structural model can also be
written as
E[Y
a
− Y
a=0
|A = a, L] = β
1
a + β
2
aL
which is referred to as a structural nested mean model. The parameters β
1
andRobins (1994) first described the
class of structural nested models.
These models are “nested” when
the treatment is time-varying. See
Part III for an explanation.
β
2
(again, a vector), which are estimated by g-estimation, quantify the average
causal effect of smoking cessation A on Y within levels of A and L.
In Chapter 13 we considered parametric models for the mean outcome Y
that, like structural nested models, were also conditional on treatment A and
covariates L. Those outcome models were the basis for standardization when
estimating the parametric g-formula. In contrast with those parametric mod-
els, structural nested models are semiparametric because they are agnostic
about both the intercept and the main effect of L—that is, there is no pa-
rameter β
0
and no parameter β
3
for a term β
3
L. As a result of leaving these
parameters unspecified, structural nested models make fewer assumptions and
can be more robust to model misspecification than the parametric g-formula.
See Fine Point 14.1 for a description of the relation between structural nested
models and the marginal structural models of Chapter 12.
In the presence of censoring, our causal effect of interest is not E[Y
a=1
−
184 G-estimation of structural nested models
Fine Point 14.1
Relation between marginal structural models and structural nested models. Consider a marginal structural mean
model for the average outcome under treatment level a within levels of a continuous covariate V , a component of L,
E[Y
a
|V ] = β
0
+ β
1
a + β
2
aV + β
3
V
The sum β
1
+ β
2
v is the average causal effect E[Y
a=1
− Y
a=0
|V = v] among individuals with V = v, and the sum
β
0
+β
3
v is the mean counterfactual outcome under no treatment E[Y
a=0
|V = v] in those individuals. Suppose the only
inferential goal is the average causal effect β
1
+β
2
v, i.e., we are not interested in estimating β
0
+β
3
v = E[Y
a=0
|V = v].
Then we would write the model as E[Y
a
|V ] = E[Y
a=0
|V ] + β
1
a + β
2
aV or, equivalently, as
E[Y
a
− Y
a=0
|V ] = β
1
a + β
2
aV
which is referred to as a semiparametric marginal structural mean model because, unlike the marginal structural models
in Chapter 12, it leaves the mean counterfactual outcomes under no treatment E[Y
a=0
|V ] completely unspecified. If
only interested in the conditional effects of A given V , semiparametric marginal structural models are more robust than
parametric ones when V is continuous or high-dimensional because misspecification of the parametric model β
0
+ β
3
V
for E[Y
a=0
|V ] may result in biased estimates of the treatment effect even when the model β
1
a + β
2
aV is correct. This
bias arises because the estimates of (β
0
, β
3
) can be correlated with the estimates of (β
1
, β
2
).
A semiparametric marginal structural model conditional on a strict subset V of the confounders L needed for ex-
changeability is identical to a structural nested model for the effect of a blip of treatment conditional on covariates V ,
such as β
1
a + β
2
aV . Therefore, to estimate β
1
and β
2
in the absence of censoring, we first create a pseudo-population
with IP weights SW
A
(V ) = f (A|V ) /f (A|L). In this pseudo-population there is only confounding by V and there-
fore the semiparametric marginal structural model is a structural nested model whose parameters are estimated by
g-estimation with V substituted by L and each individual’s contribution weighted by SW
A
(V ).
Consider the special case of a semiparametric marginal structural mean model within levels of all variables in L,
rather than only a subset V so that SW
A
(V ) are equal to 1 for all individuals. That is, let us consider the model
E[Y
a
−Y
a=0
|L] = β
1
a+β
2
aL, which we refer to as a faux semiparametric marginal structural model. Under conditional
exchangeability, this model is the structural nested mean model we use in this chapter.
Y
a=0
|A, L] but E[Y
a=1,c=0
− Y
a=0,c=0
|A, L], i.e., the average causal effect if
everybody had remained uncensored. Estimating this difference requires ad-
justment for both confounding and selection bias (due to censoring C = 1)
for the effect of treatment A. As described in the previous two chapters, IP
weighting and standardization can be used to adjust for these two biases. G-
estimation, on the other hand, can only be used to adjust for confounding, not
selection bias. Thus, when using g-estimation, one first needs to adjust for se-Technically, IP weighting is not nec-
essary to adjust for selection bias
when using g-estimation with a
time-fixed (as opposed to a time-
varying) treatment that does not
affect any variable in L, and an
outcome measured at a single time
point. That is, if as we have been
assuming Y
a
⊥⊥(A, C) |L, we can
apply g-estimation to the uncen-
sored subjects without having to
use IP weights.
lection bias due to censoring by IP weighting. In practice, we can first estimate
nonstabilized IP weights for censoring to create a pseudo-population in which
nobody is censored, and then apply g-estimation to the pseudo-population.
In our smoking cessation example, we can use the nonstabilized IP weights
W
C
= 1/ Pr [C = 0|L, A] that we estimated in Chapter 12. Again we assume
that the vector of variables L is sufficient to adjust for both confounding and
selection bias.
All the g-estimation analyses described in this chapter incorporate IP weights
to adjust for the potential selection bias due to censoring. Under the assump-
tion that the censored and the uncensored are exchangeable conditional on the
measured covariates L, the structural nested mean model E[Y
a
− Y
a=0
|A =
14.4 Rank preservation 185
Technical Point 14.1
Multiplicative structural nested mean models. In the text we only consider additive structural nested mean models.
When the outcome variable Y can only take positive values, a multiplicative structural nested mean model is often
preferred. An example of a multiplicative structural nested mean model is
log
E[Y
a
|A = a, L]
E[Y
a=0
|A = a, L]
= β
1
a + β
2
aL
which can be fit by g-estimation, as described in Section 14.5, with H(ψ
†
) defined to be Y exp
h
−ψ
†
1
a − ψ
†
2
aL
i
.
Originally, the above multiplicative model could only be used for a binary (0, 1) outcome variable Y when the
probability of Y = 1 was small in all strata of L, which prevented the model from predicting probabilities greater
than 1. Richardson, Robins and Wang (2017) overcome this rare outcome restriction by replacing the baseline risk
Pr[Y = 1|A = 0, L] as the nuisance parameter with the conditional log-odds product. Also, these authors generalized
multiplicative structural nested mean models for rare binary outcomes to time-varying treatments and used g-estimation
to construct doubly robust estimators of the causal parameters (Wang et al. 2022). Before these developments, in the
setting of a non-rare binary outcome Y it had been suggested to fit a structural nested logistic model such as
logit Pr[Y
a
= 1|A = a, L] − logit Pr[Y
a=0
= 1|A = a, L] = β
1
a + β
2
aL
However, structural nested logistic models have two major drawbacks. First, the model is not collapsible, i.e., the
marginal causal odds ratio is not a weighted average of the conditional causal odds ratios (Fine Point 4.3). Second,
the model does not generalize easily to time-varying treatments. For details, see Robins (1999) and Tchetgen Tchetgen
and Rotnitzky (2011).
a, L] = β
1
a + β
2
aL, when applied to the pseudo-population created by the IP
weights W
C
, is really a structural model in the absence of censoring:
E[Y
a,c=0
− Y
a=0,c=0
|A = a, L] = β
1
a + β
2
aL
For simplicity, we will omit the superscript c = 0 hereafter in this chapter.
In this chapter we will use g-estimation of a structural nested mean model
to estimate the effect of the dichotomous treatment “smoking cessation”, but
structural nested models can also be used for continuous treatment variables—
like “change in smoking intensity” (see Chapter 12). For continuous variables,
the model needs to specify the dose-response function for the effect of treatment
A on the mean outcome Y . For example, E[Y
a
−Y
a=0
|A = a, L] = β
1
a+β
2
a
2
+
β
3
aL+β
4
a
2
L, or E[Y
a
−Y
a=0
|A = a, L] could be a smooth function splines, of
A and L. For a discussion of structural nested mean models for dichotomous
outcomes, see Technical Point 14.1.
We now turn our attention to the concept of rank preservation, which will
help us describe g-estimation of structural nested models.
14.4 Rank preservation
In our smoking cessation example, all individuals can be ranked according to
the value of their observed outcome Y . Subject 23522 is ranked first withcode: Program 14.1
weight gain of 48.5 kg, individual 6928 is ranked second with weight gain 47.5
kg... and individual 23321 is ranked last with weight gain of −41.3 kg. Simi-
larly we could think of ranking all individuals according to the value of their
186 G-estimation of structural nested models
counterfactual outcome under treatment Y
a=1
if the value of Y
a=1
were known
for all individuals rather than only for those who were actually treated. Sup-
pose for a second that we could actually rank everybody according to Y
a=1
and
also according to Y
a=0
. We would then have two lists of individuals ordered
from larger to smaller value of the corresponding counterfactual outcome. If
both lists are in identical order we say that there is rank preservation.
When the effect of treatment A on the outcome Y is exactly the same,
on the additive scale, for all individuals in the study population, we say that
additive rank preservation holds. For example, if smoking cessation increases
everybody’s body weight by exactly 3 kg, then the ranking of individuals ac-
cording to Y
a=0
would be equal to the ranking according to Y
a=1
, except
that in the latter list all individuals will be 3 kg heavier. A particular case of
additive rank preservation occurs when the sharp null hypothesis is true (see
Chapter 1), i.e., if treatment has no effect on the outcomes of any individual in
the study population. For the purposes of structural nested mean models we
will care about additive rank preservation within levels of L. This conditional
additive rank preservation holds if the effect of treatment A on the outcome Y
Figure 14.1
is exactly the same for all individuals with the same values of L.
An example of an (additive conditional) rank-preserving structural model
is
Y
a
i
− Y
a=0
i
= ψ
1
a + ψ
2
aL
i
for all individuals i
where ψ
1
+ ψ
2
l is the constant causal effect for all individuals with covariate
values L = l. That is, for every individual i with L = l, the value of Y
a=1
i
is
equal to Y
a=0
i
+ ψ
1
+ ψ
2
l. An individual’s counterfactual outcome under no
treatment Y
a=0
i
is shifted by ψ
1
+ ψ
2
l to obtain the value of her counterfactual
outcome under treatment. Figure 14.1 shows an example of additive rank
Figure 14.2
Figure 14.3
preservation within the stratum L = l. The bell-shaped curves represent the
distribution of the counterfactual outcomes Y
a=0
(left curve) and Y
a=1
(right
curve). The two dots in the upper part of the figure represent the values of
the two counterfactual outcomes for individual i, and the two dots in the lower
part represent the values of the two counterfactual outcomes for individual j.
The arrows represent the shifts from Y
a=0
to Y
a=1
, which are equal to
ψ
1
+ ψ
2
l for all individuals in this stratum. Figure 14.2 shows an example
of rank preservation within another stratum L = l
′
. The distribution of the
counterfactual outcomes is different from that in stratum L = l. For example,
the mean of Y
a=0
in Figure 14.1 is to the left of the mean of Y
a=0
in Figure
14.2, which means that, on average, individuals in stratum L = l have a smaller
weight gain under no smoking cessation than individuals in stratum L = l
′
.
The shift from Y
a=0
to Y
a=1
is ψ
1
+ ψ
2
l
′
for all individuals with L = l
′
, as
shown for individuals p and q.
For most treatments and outcomes, the individual causal effect is not ex-
pected to be constant—not even approximately constant—across individuals
with the same covariate values, and thus (additive conditional) rank preserva-
tion is scientifically implausible. In our example we do not expect that smoking
cessation affects equally the body weight of all individuals with the same val-
ues of L. Some people are—genetically or otherwise—more susceptible to the
effects of smoking cessation than others, even within levels of the covariates
L. The individual causal effect of smoking cessation will vary across people:
after quitting smoking some individuals will gain a lot of weight, some will
gain little, and others may even lose some weight. Reality may look more like
the situation depicted in Figure 14.3, in which the shift from Y
a=0
to Y
a=1
varies across individuals with the same covariate values, and even ranks are
14.5 G-estimation 187
not preserved since the outcome for individual i is less than that for individual
j when a = 0 but not when a = 1.
Because of the implausibility of rank preservation, one should not generally
use methods for causal inference that rely on it. In fact none of the methods
we consider in this book require rank preservation. For example, the marginal
structural mean models from Chapter 12 are models for average causal effects,
not for individual causal effects, and thus they do not assume rank preservation.
The estimated average causal effect of smoking cessation on weight gain was
3.5 kg (95% confidence interval: 2.5, 4.5). This average effect is agnostic as
to whether rank preservation of individual causal effects holds. Similarly, the
structural nested mean model in the previous section made no assumptions
about rank preservation.
The additive rank-preserving model in this section makes a much strongerA structural nested mean model
is well defined in the absence of
rank preservation. For example,
for the setting depicted in Figure
14.3, one could propose a model
to estimate the average causal ef-
fect within strata of L, even when
the treatment effects of individuals
with the same value of L are not all
identical.
assumption than non-rank-preserving models: the assumption of constant treat-
ment effect for all individuals with the same value of L. There is no reason
why we would want to use such an unrealistic rank-preserving model in prac-
tice. And yet we use it in the next section to introduce g-estimation because
g-estimation is easier to understand for rank-preserving models, and because
the g-estimation procedure is actually the same for rank-preserving and non-
rank-preserving models. Note that the (conditional additive) rank-preserving
structural model is a structural mean model—the mean of the individual shifts
from Y
a=0
to Y
a=1
is equal to each of the individual shifts within levels of L.
14.5 G-estimation
This section links the material in the previous three sections. Suppose the
goal is estimating the parameters of the structural nested mean model E[Y
a
−
Y
a=0
|A = a, L] = β
1
a. For simplicity, we first consider a model with a single
parameter β
1
. Because the model lacks product terms β
2
aL, we are effectively
assuming that the average causal effect of smoking cessation is constant across
strata of L, i.e., no additive effect modification by L.
We also assume that the additive rank-preserving model Y
a
i
−Y
a=0
i
= ψ
1
a
is correctly specified for all individuals i. Then the individual causal effect ψ
1
is equal to the average causal effect β
1
in which we are interested. We write
the rank-preserving model as Y
a
−Y
a=0
= ψ
1
a, without a subscript i to index
individuals because the model is the same for all individuals. For reasons that
will soon be obvious, we write the model in the equivalent form
Y
a=0
= Y
a
− ψ
1
a
The first step in g-estimation is linking the model to the observed data. To
do so, remember that an individual’s observed outcome Y is, by consistency,
the counterfactual outcome Y
a=1
if the person received treatment A = 1 or
the counterfactual outcome Y
a=0
if the person received no treatment A = 0.
Therefore, if we replace the fixed value a in the structural model by each
individual’s value A—which will be 1 for some and 0 for others—then we can
replace the counterfactual outcome Y
a
by the individual’s observed outcome
Y
A
= Y .
The rank-preserving structural model then implies an equation in which
each individual’s counterfactual outcome Y
a=0
is a function of his observed
188 G-estimation of structural nested models
data on treatment and outcome and the unknown parameter ψ
1
:
Y
a=0
= Y − ψ
1
A
If this model were correct and we knew the value of ψ
1
then we could calculate
the counterfactual outcome under no treatment Y
a=0
for each individual in
the study population. But we don’t know ψ
1
. Estimating it is precisely the
goal of our analysis.
Let us play a game. Suppose a friend of yours knows the value of ψ
1
but he
only tells you that ψ
1
is one of the following: ψ
†
= −20, ψ
†
= 0, or ψ
†
= 10.
He challenges you: “Can you identify the true value ψ
1
among the 3 possible
values ψ
†
?” You accept the challenge. For each individual, you compute
H(ψ
†
) = Y − ψ
†
A
for each of the three possible values ψ
†
. The newly created variables H(−20),
H(0), and H(10) are candidate counterfactuals. Only one of them is the coun-
terfactual outcome Y
a=0
. More specifically, H(ψ
†
) = Y
a=0
if ψ
†
= ψ
1
. In
this game, choosing the correct value of ψ
1
is equivalent to choosing which
one of the three candidate counterfactuals H(ψ
†
) is the true counterfactual
Y
a=0
= H(ψ
1
). Can you think of a way to choose the right H(ψ
†
)?
Remember from Section 14.2 that the assumption of conditional exchange-
ability can be expressed as a logistic model for treatment given the counterfac-
tual outcome and the covariates L. When conditional exchangeability holds,
the parameter α
1
for the counterfactual outcome should be zero. So we haveRosenbaum (1987) proposed a ver-
sion of this procedure for non-time-
varying treatments.
a simple method to choose the true counterfactual out of the three variables
H(ψ
†
). We fit three separate logistic models
logit Pr[A = 1|H(ψ
†
), L] = α
0
+ α
1
H(ψ
†
) + α
2
L,
one per each of the three candidates H(ψ
†
). The candidate H(ψ
†
) with α
1
= 0
is the counterfactual Y
a=0
, and the corresponding ψ
†
is the true value ψ
1
. ForImportant: G-estimation does not
test whether conditional exchange-
ability holds; it assumes that condi-
tional exchangeability holds.
example, suppose that H(ψ
†
= 10) is unassociated with treatment A given
the covariates L. Then our estimate
ˆ
ψ
1
of ψ
1
is 10. We are done. That was
g-estimation.
In practice, however, we need to g-estimate the parameter ψ
1
in the absence
of a friend who knows the right answer and likes to play games. Therefore we
will need to search over all possible values ψ
†
until we find the one that results
in an H(ψ
†
) with α
1
= 0. Because not all possible values can be tested—there
is an infinite number of values ψ
†
in any given interval—we can conduct a fine
search over the possible range of ψ
†
values from −20 to 20 by increments of
0.01. The finer the search, the closer to the true estimate
ˆ
ψ
1
we will get, but
also the greater the computational demands.code: Program 14.2
In our smoking cessation example, we first computed each individual’s value
of the 31 candidates H(2.0), H(2.1), H(2.2), ...H(4.9), and H(5.0) for values
ψ
†
between 2.0 and 5.0 by increments of 0.1. We then fit 31 separate logistic
models for the probability of smoking cessation. These models were exactly
like the one used to estimate the denominator of the IP weights in Chapter
12, except that we added to each model one of the 31 candidates H(ψ
†
).
The parameter estimate ˆα
1
for H(ψ
†
) was closest to zero for values H(3.4)
and H(3.5). A finer search found that the minimum value of ˆα
1
(which was
essentially zero) was for H(3.446). Thus, our g-estimate
ˆ
ψ
1
of the average
causal effect ψ
1
= β
1
of smoking cessation on weight gain is 3.4 kg.
To compute a 95% confidence interval around our g-estimate of 3.4, we
used the P-value for a Wald test of α
1
= 0 in the logistic models fit above.
14.5 G-estimation 189
Fine Point 14.2
Sensitivity analysis for unmeasured confounding. G-estimation relies on the fact that α
1
= 0 if conditional
exchangeability given L holds. Now consider a setting in which conditional exchangeability does not hold. For example,
suppose that the probability of quitting smoking A is lower for individuals whose spouse is a smoker, and that the
spouse’s smoking status is associated with important determinants of weight gain Y not included in L. That is,
there is unmeasured confounding by spouse’s smoking status. Because now the variables in L are insufficient to achieve
exchangeability of the treated and the untreated, the treatment A and the counterfactual Y
a=0
are associated conditional
on L. That is, α
1
= 0 and we cannot apply g-estimation as described in the main text.
But g-estimation does not require that α
1
= 0. Suppose that, because of unmeasured confounding by the spouse’s
smoking status, α
1
is expected to be 0.1 rather than 0. Then we can apply g-estimation as described in the text
except that we will test whether α
1
= 0.1 rather than whether α
1
= 0. G-estimation does not require that conditional
exchangeability given L holds, but that the magnitude of nonexchangeability—the value of α
1
—is known. This property
of g-estimation can be used to conduct sensitivity analyses for unmeasured confounding.
If we believe that L may not sufficiently adjust for confounding, then we can repeat our g-estimation analysis under
different scenarios of unmeasured confounding, represented by a range of values of α
1
, and plot the effect estimates
under each of them. Such plot shows how sensitive our effect estimate is to unmeasured confounding of different
direction and magnitude. One practical problem for this approach is how to quantify the unmeasured confounding on
the α
1
scale (is 0.1 a lot of unmeasured confounding?) Robins, Rotnitzky, and Scharfstein (1999) provide technical
details on sensitivity analysis for unmeasured confounding using g-estimation.
As expected, the P-value was 1—it was actually 0.998—for ψ
†
= 3.446, whichAny valid test other than the Wald
may be used. For example, a
Score test simplifies the calcula-
tions (it doesn’t require fitting mul-
tiple models) and, in large samples,
is essentially equivalent to a Wald
test.
is the value ψ
†
that results in a candidate H(ψ
†
) with a parameter estimate
ˆα
1
= 0. Of the 31 logistic models that we fit for ψ
†
values between 2.0 and 5.0,
the P-value was greater than 0.05 in all models with H(ψ
†
) based on ψ
†
values
between approximately 2.5 and 4.5. That is, using the conventional statistical
jargon, the test “did not reject the null hypothesis” at the 5% level for the
subset of ψ
†
values between 2.5 and 4.5. By inverting the test results, we
concluded that the limits of the 95% confidence interval around 3.4 are 2.5 and
4.5. Another option to compute the 95% confidence interval is bootstrapping
of the g-estimation procedure.
More generally, the 95% confidence interval for a g-estimate is determined
by finding the set of values of ψ
†
that result in a P-value> 0.05 when testing for
α
1
= 0. The 95% confidence interval is obtained by inversion of the statistical
test for α
1
= 0, with the limits of the 95% confidence interval being the limits
of the set of values ψ
†
with P-value> 0.05. In our example, the statistical test
was based on a robust variance estimator because of the use of IP weighting toIn the presence of censoring, the fit
of the logistic models is necessar-
ily restricted to uncensored individ-
uals (C = 0), and the contribution
of each individual is weighted by
the estimate of the individual’s IP
weight SW
C
. See Technical Point
14.2.
adjust for censoring. Therefore our 95% confidence interval is conservative in
large samples, i.e., it will trap the true value at least 95% of the time. In large
samples, bootstrapping would result in a non-conservative, and thus possibly
narrower, 95% confidence interval for the g-estimate.
Back to non-rank-preserving models. The g-estimation algorithm (i.e., the
computer code implementing the procedure) for ψ
1
produces a consistent es-
timate of the parameter β
1
of the mean model, assuming the mean model is
correctly specified (that is, if the average treatment effect is equal in all levels
of L). This is true regardless of whether the individual treatment effect is
constant, i.e., regardless of whether the conditional additive rank preservation
holds. In other words, the validity of the g-estimation algorithm does not actu-
ally require that H(β
1
) = Y
a=0
for all individuals, where β
1
is the parameter
value in the mean model. Rather, the algorithm only requires that H(β
1
) and
190 G-estimation of structural nested models
Y
a=0
have the same conditional mean given L.
Interestingly, the above g-estimation procedure can be readily modified to
incorporate a sensitivity analysis for unmeasured confounding, as described in
Fine Point 14.2.
14.6 Structural nested models with two or more parameters
We have so far considered a structural nested mean model with a single pa-
rameter β
1
. The lack of product terms β
2
aL implies that we believe that the
average causal effect of smoking cessation does not vary across strata of L. The
structural nested model will be misspecified—and thus our causal inferences
will be wrong—if there is indeed effect modification by some components V of
L but we failed to add a product term β
2
aV . This is in contrast with the sat-
urated marginal structural model E[Y
a
] = β
0
+ β
1
a, which is not misspecified
if we fail to add terms β
2
aV and β
3
V even if there is effect modification by V .
Marginal structural models that do not condition on V estimate the average
causal effect in the population, whereas those that condition on V estimate theAs discussed in Chapter 12, a de-
sirable property of marginal struc-
tural models is null preservation:
when the null hypothesis of no aver-
age causal effect is true, the model
is never misspecified. Structural
nested models preserve the null too.
In contrast, although the paramet-
ric g-formula preserves the null for
time-fixed treatments, it loses this
property in the time-varying setting
(see Part III).
average causal effect within levels of V . Structural nested models estimate, by
definition, the average causal effect within levels of the covariates L, not the
average causal effect in the population. Omitting product terms in structural
nested models when there is effect modification will generally lead to bias due
to model misspecification.
Fortunately, the g-estimation procedure described in the previous section
can be generalized to models with product terms. For example, suppose we
believe that the average causal effect of smoking cessation depends on the base-
line level of smoking intensity V . We may then consider the structural nested
mean model E[Y
a
− Y
a=0
|A = a, L] = β
1
a + β
2
aV . Because the structural
model has two parameters, β
1
and β
2
, we also need to include two parameters
in the IP weighted logistic model for Pr[A = 1|H(β
†
), L] with β
†
=
β
†
1
, β
†
2
and H(β
†
) = Y − β
†
1
A − β
†
2
AV . For example, we could fit the logistic model
logit Pr[A = 1|H(β
†
), L] = α
0
+ α
1
H(β
†
) + α
2
H(β
†
)V + α
3
L
and find the combination of values of β
†
1
and β
†
2
that result in a H(β
†
) that is
independent of treatment A conditional on the covariates L. That is, we need
to search the combination of values β
†
1
and β
†
2
that make both α
1
and α
2
equal
to zero. Because the model has two parameters, the search must be conducted
over a two-dimensional space. Thus a systematic, brute force search will be
more involved than that described in the previous section.
However, even though we motivated g-estimation by using a parameter
search, a search over the possible values of the parameters is not generally nec-
essary for g-estimation. In fact, for linear mean models like the one discussed
here, the estimate can be directly calculated using a formula, i.e., the estima-
tor has closed form . For nonlinear structural nested mean models, no closed
form estimator exists but we can use standard optimization techniques based
on derivatives, such as Newton-Raphson, because g-estimation can be seen as
solving an estimating equation for the model parameters (see Technical Point
14.2 for details). For certain structural nested models for survival analysis, a
search is required because the estimating equation is not differentiable with
respect to the model parameters (see Chapter 17).
14.6 Structural nested models with two or more parameters 191
In our smoking cessation example, the g-estimates were
ˆ
β
1
= 2.86 and
ˆ
β
2
=code: Program 14.3
0.03. The corresponding 95% confidence intervals can most easily be calculated
by bootstrapping. In the more general case, we would consider a model that
allows the average causal effect of smoking cessation to vary across all strata of
the variables in L. For a dichotomous treatment, the unsaturated linear model
E[Y
a
−Y
a=0
] = β
1
a + a
P
p
j=1
β
2j
L
j
has p + 1 parameters β
1
, β
21,...
β
2p
, where
β
2j
is the parameter corresponding to the product term aL
j
and L
j
represents
one of the p components of L. The average causal effect in the entire study
population can then be calculated as β
1
+
1
n
P
i
P
p
j=1
β
2j
L
ij
, where n is the
number of individuals in the study.
After having described g-methods, we now review two methods that are
arguably the most commonly used approaches to adjust for confounding: out-
come regression and propensity scores.
192 G-estimation of structural nested models
Technical Point 14.2
G-estimation of structural nested mean models. Consider the structural nested mean model
E
Y − Y
a=0
|A, L
= Aγ (L; β)
where γ
L; β
†
is a known function, β
†
is usually a vector-valued parameter, and γ
L; β
†
= 0
= 0. An asymptotically
unbiased and normally distributed estimate of β can be obtained by g-estimation under the assumptions described in the
text, including a correctly specified parametric model for E [A|L] . Specifically, our estimate of β is the value of β
†
that
minimizes the association between H(β
†
) = Y −Aγ
L; β
†
and A conditional on L. When we base our g-estimate on
the score test (see, e.g., Casella and Berger 2002), this procedure is equivalent to finding the parameter value β
†
that
solves the estimating equation
n
X
i=1
I [C
i
= 0] W
C
i
H
i
(β
†
) (A
i
− E [A|L
i
]) q(L
i
) = 0
where q(L
i
) is a (user-specified) vector function of the same dimension as β, I [C
i
= 0] is an indicator for censoring
for individual i, and the IP weight W
C
i
and the expectation E [A|L
i
] = Pr [A = 1|L
i
] are replaced by their estimates.
E [A|L
i
] can be estimated from a logistic model for treatment conditional on the covariates L in which individual i’s
contribution is weighted by W
C
i
if C
i
= 0 and it is zero otherwise. [Because A and L are observed on all individuals,
we could also estimate E [A|L
i
] by an unweighted logistic regression of A on L using all individuals.] The choice of
the vector function q(L
i
) affects the statistical efficiency of the estimator, but not its consistency. That is, although all
choices of the function will result in valid confidence intervals, the length of the confidence interval will depend on the
function. Robins (1994) provided a formal description of structural nested mean models, and derived the function that
minimizes confidence interval length.
The solution to the equation has a closed form when γ
L; β
†
is linear in β
†
, i.e., γ
L; β
†
= β
†,T
d(L) for a known
vector function d(L) of the same dimension as β. In that case, if we choose q(L) = d(L),
ˆ
β equals
n
X
i=1
I [C
i
= 0] W
C
i
A
i
(A
i
− E [A|L
i
]) d(L
i
)d(L
i
)
T
!
−1
n
X
i=1
I [C
i
= 0] W
C
i
Y
i
(A
i
− E [A|L
i
]) d(L
i
)
A natural question is whether we can increase statistical efficiency by replacing H
i
(β
†
) by a nonlinear function, such
as
H
i
(β
†
)
3
, in the above estimating equation and still preserve consistency of the estimate. Nonlinear functions of
H
i
(β
†
) cannot be used in our estimating equation for models that, like the structural nested mean models described in
this chapter, impose only mean independence conditional on L, i.e., E [H(β
1
)|A, L] = E [H(β
1
)|L], for identification.
Nonlinear functions of H
i
(β
†
) can be used for models that impose distributional independence, i.e., H(β
1
)⊥⊥A|L, like
structural nested distribution models (not described in this chapter) that map percentiles of the distribution of Y
a
given
(A = a, L) into percentiles of the distribution of Y
0
given (A = a, L).
The estimator of β is consistent only if the models used to estimate E [A|L] and Pr [C = 1|A, L] are both correct. We
can construct a more robust estimator by replacing H(β
†
) by H(β
†
)−E
H(β
†
)|L
in the estimating equation, and then
estimating the latter conditional expectation by fitting an unweighted linear model for E
H(β
†
)|L
= E
Y
a=0
|L
among
the uncensored individuals. If this model is correct then the estimate of β solving the modified estimating equation
remains consistent even if both the above models for E [A|L] and Pr [C = 1|A, L] are incorrect. Thus we obtain a
consistent estimator of β if either (i) the model for E
H(β
†
)|L
or (ii) both models for E [A|L] and Pr [C = 1|A, L] are
correct, without knowing which of (i) or (ii) is correct. We refer to such an estimator as being doubly robust.Technical
Point 21.6 describes the closed-form of this doubly robust estimator for the linear structural nested mean model with
time-varying treatments (see Robins 2000).
Chapter 15
OUTCOME REGRESSION AND PROPENSITY SCORES
Outcome regression and various versions of propensity score analyses are the most commonly used parametric
methods for causal inference. You may rightly wonder why it took us so long to include a chapter that discusses
these methods. So far we have described IP weighting, standardization, and g-estimation—the g-methods. Pre-
senting the most commonly used methods after the least commonly used ones seems an odd choice on our part.
Why didn’t we start with the simpler and widely used methods based on outcome regression and propensity scores?
Because these methods do not work in general.
More precisely, the simpler outcome regression and propensity score methods—as described in a zillion publi-
cations that this chapter cannot possibly summarize—work fine in simpler settings, but these methods are not
designed to handle the complexities associated with causal inference with time-varying treatments. In Part III
we will again discuss g-methods but will say less about conventional outcome regression and propensity score
methods. This chapter is devoted to causal methods that are commonly used but have limited applicability for
complex longitudinal data.
15.1 Outcome regression
In the last three chapters we have described IP weighting, standardization,
and g-estimation to estimate the average causal effect of smoking cessation
(the treatment) A on weight gain (the outcome) Y . We also described how toReminder: We defined the aver-
age causal effect as E[Y
a=1,c=0
] −
E[Y
a=0,c=0
]. We assumed that
exchangeability of the treated and
the untreated was achieved condi-
tional on the L variables sex, age,
race, education, intensity and dura-
tion of smoking, physical activity in
daily life, recreational exercise, and
weight.
estimate the average causal effect within subsets of the population, either by
restricting the analysis to the subset of interest or by adding product terms in
marginal structural models (Chapter 12) and structural nested models (Chap-
ter 14). Take structural nested models. These models include parameters for
the product terms between treatment A and the variables L, but no parame-
ters for the variables L themselves. This is an attractive property of structural
nested models because we are interested in the causal effect of A on Y within
levels of L but not in the (noncausal) relation between L and Y . A method—
g-estimation of structural nested models—that is agnostic about the functional
form of the L-Y relation is protected from bias due to misspecifying this rela-
tion.
On the other hand, if we were willing to specify the L-Y association within
levels of A, we would consider the structural modelIn Chapter 12, we referred to this
model as a faux marginal structural
model because it has the form of
a marginal structural model but IP
weighting is not required to esti-
mate its parameters. The stabilized
IP weights SW
A
(L) are all equal to
1 because the model is conditional
on the entire vector L rather than
on a subset V of L.
E[Y
a,c=0
|L] = β
0
+ β
1
a + β
2
aL + β
3
L
where β
2
and β
3
are vector parameters. The average causal effects of smoking
cessation A on weight gain Y in each stratum of L are a function of β
1
and β
2
,
the mean counterfactual outcomes under no treatment in each stratum of L
are a function of β
0
and β
3
. The parameter β
3
is usually referred as the main
effect of L, but the use of the word effect is misleading because β
3
may not
have an interpretation as the causal effect of L (there may be confounding for
L). The parameter β
3
simply quantifies how the mean of the counterfactual
Y
a=0,c=0
varies as a function of L, as we can see in our structural model. See
194 Outcome regression and propensity scores
Fine Point 15.1
Nuisance parameters. Suppose our goal is to estimate the causal parameters β
1
and β
2
. If we do so by fitting the
outcome regression model E[Y
a,c=0
|L] = β
0
+β
1
a+β
2
aL+β
3
L, our estimates of β
1
and β
2
will in general be consistent
only if β
0
+ β
3
L correctly models the dependence of the mean E[Y
a=0,c=0
|L] on L. We refer to the parameters β
0
and
β
3
as nuisance parameters because they are not our parameters of primary interest.
On the other hand, if we estimate β
1
and β
2
by g-estimation of the structural nested model E[Y
a,c=0
−Y
a=0,c=0
|L] =
β
1
a + β
2
aL, then our estimates of β
1
and β
2
will in general be consistent only if the conditional probability of treatment
given L Pr[A = 1|L] is correct. That is, the parameters of the treatment model such as logit Pr[A = 1|L] = α
0
+ α
1
L
are now the nuisance parameters.
For example, bias would arise in the outcome regression model if a covariate L is modeled with a linear term β
3
L
when it should actually be linear and quadratic β
3
L+β
4
L
2
. Structural nested models are not subject to misspecification
of an outcome regression model because the L-Y relation is not specified in the structural model. However, bias would
arise when using g-estimation of structural nested models if the L-A relation is misspecified in the treatment model.
Symmetrically, outcome regression models are not subject to misspecification of a treatment model. For fixed treatments
that do not vary over time, deciding what method to use boils down to deciding which nuisance parameters—those in
the outcome model or in the treatment model—we believe can be more accurately estimated. When possible, a better
alternative is to use doubly robust methods (see Fine Point 13.2).
Fine Point 15.1 for a discussion of parameters that, like β
0
and β
3
, do not have
a causal interpretation.
The counterfactual mean outcomes if everybody in stratum l of L had been
treated and remained uncensored, E[Y
a=1,c=0
|L = l], are equal to the corre-
sponding mean outcomes in the uncensored treated, E[Y |A = 1, C = 0, L = l],
under exchangeability, positivity, and well-defined interventions. And analo-
gously for the untreated. Therefore the parameters of the above structural
model can be estimated via ordinary least squares by fitting the outcome re-
gression model
E[Y |A, C = 0, L] = α
0
+ α
1
A + α
2
AL + α
3
L
as described in Section 13.2. Like stratification in Chapter 3, outcome regres-
sion adjusts for confounding by estimating the causal effect of treatment in
each stratum of L. If the variables L are sufficient to adjust for confounding
(and selection bias) and the outcome model is correctly specified, no further
adjustment is needed. That is, the parameters α of the regression model equal
the parameters β of the structural model.β
0
and β
3
specify the dependence
of Y
a=0,c=0
on L, which is required
when the model is used to esti-
mate (i) the mean counterfactual
outcomes and (ii) the conditional
(within levels of L) effect on the
multiplicative rather than additive
scale.
In Section 13.2, outcome regression was an intermediate step towards the
estimation of a standardized outcome mean. Here, outcome regression is the
end of the procedure. Rather than standardizing the estimates of the condi-
tional means to estimate a marginal mean, we just compare the conditional
mean estimates. In Section 13.2, we fit a regression model with only one prod-
uct term in β
2
(between A and smoking intensity). That is, a model in which
we a priori set most product terms equal to zero. Using the same model as in
Section 13.2, here we obtained the parameter estimates
ˆ
β
1
= 2.6 and
ˆ
β
2
= 0.05.
As an example, the effect estimate
b
E[Y |A = 1, C = 0, L]−
b
E[Y |A = 0, C = 0, L]
was 2.8 (95% confidence interval: 1.5, 4.1) for those smoking 5 cigarettes/day,code: Program 15.1
and 4.4 (95% confidence interval: 2.8, 6.1) for 40 cigarettes/day. A common
approach to outcome regression is to assume that there is no effect modification
by any variable in L. Then the model is fit without any product terms and
ˆ
β
1
is an estimate of both the conditional and marginal average causal effects
15.2 Propensity scores 195
of treatment. In our example, a model without any product terms yielded the
estimate 3.5 (95% confidence interval: 2.6, 4.3) kg.
In this chapter we did not need to explain how to fit an outcome regression
model because we had already done it in Chapter 13 when estimating the
components of the parametric g-formula. It is equally straightforward to use
outcome regression for discrete outcomes. For a dichotomous outcome Y one
could fit a logistic model for Pr [Y = 1|A = a, C = 0, L].
15.2 Propensity scores
When using IP weighting (Chapter 12) and g-estimation (Chapter 14), we
estimated the probability of treatment given the covariates L, Pr [A = 1|L],
for each individual. Let us refer to this conditional probability as π(L). The
value of π(L) is close to 0 for individuals who have a low probability of receiving
treatment and is close to 1 for those who have a high probability of receiving
treatment. That is, π(L) measures the propensity of individuals to receive
treatment given the information available in the covariates L. No wonder that
π(L) is referred to as the propensity score.
In an ideal randomized trial in which half of the individuals are assigned
to treatment A = 1, the propensity score π(L) = 0.5 for all individuals. Alsocode: Program 15.2
Here we only consider propensity
scores for dichotomous treatments.
Propensity score methods, other
than IP weighting and g-estimation
and other related doubly-robust es-
timators, are difficult to generalize
to non-dichotomous treatments.
note that π(L) = 0.5 for any choice of L. In contrast, in observational studies
some individuals may be more likely to receive treatment than others. Be-
cause treatment assignment is beyond the control of the investigators, the true
propensity score π(L) is unknown, and therefore needs to be estimated from
the data.
In our example, we can estimate the propensity score π(L) by fitting a
logistic model for the probability of quitting smoking A conditional on the
covariates L. This is the same model that we used for IP weighting and g-
estimation. Under this model, individual 22941 was estimated to have the
lowest estimated propensity score (0.053), and individual 24949 the highest
Figure 15.1
(0.793). Figure 15.1 shows the distribution of the estimated propensity score
in quitters A = 1 (bottom) and nonquitters A = 0 (top). As expected, those
who quit smoking had, on average, a greater estimated probability of quitting
(0.312) than those who did not quit (0.245). If the distribution of π(L) were
the same for the treated A = 1 and the untreated A = 0, then there would be
no confounding due to L, i.e., there would be no open path from L to A on a
causal diagram.
Individuals with the same propensity score π(L) will generally have different
values of some covariates L. For example, two individuals with π(L) = 0.2
may differ with respect to smoking intensity and exercise, and yet they may
be equally likely to quit smoking given all the variables in L. That is, both
individuals have the same conditional probability of ending up in the treated
group A = 1. If we consider all individuals with a given value of π(L) in the
super-population, this group will include individuals with different values of LIn the study population, due
to sampling variability, the true
propensity score only approximately
“balances” the covariates L. The
estimated propensity score based
on a correct model gives better bal-
ance in general.
(e.g., different values of smoking intensity and exercise), but the distribution
of L will be the same in the treated and the untreated, that is, A⊥⊥L|π(L).
We say the propensity score balances the covariates between the treated and
the untreated.
Of course, the propensity score only balances the measured covariates L,
which does not prevent residual confounding by unmeasured factors. Random-
ization balances both the measured and the unmeasured covariates, and thus
196 Outcome regression and propensity scores
Technical Point 15.1
Balancing scores and prognostic scores. As discussed in the text, the propensity score π(L) balances the covariates
between the treated and the untreated. In fact, the propensity score π(L) is the simplest example of a balancing score.
More generally, a balancing score b(L) is any function of the covariates L such that A⊥⊥L|b(L). That is, for each value
of the balancing score, the distribution of the covariates L is the same in the treated and the untreated. Rosenbaum and
Rubin (1983) proved that exchangeability and positivity based on the variables L implies exchangeability and positivity
based on a balancing score b(L). If it is sufficient to adjust for L, then it is sufficient to adjust for a balancing score
b(L), including the propensity score π(L). The causal diagram in Figure 15.2 depicts the propensity score for the setting
represented in Figure 7.1: the π(L) can be viewed as an intermediate node between L and A with a deterministic arrow
from L to π(L). By noting that π(L) blocks all backdoor paths from A to L we have given a proof of the sufficiency
of adjusting for π(L).
An alternative to a balancing score b(L) is a prognostic score s(L), i.e., a function of the covariates L such that
Y
a=0
⊥⊥L|s(L). Adjustment methods can be developed for both balancing scores and prognostic scores, but methods for
prognostic scores require stronger assumptions and cannot be readily extended to time-varying treatments. See Hansen
(2008) and Abadie et al. (2013) for a discussion of prognostic scores.
it is the preferred method to eliminate confounding. See Technical Point 15.1
for a formal definition of a balancing score.
Like all methods for causal inference that we have discussed, the use of
propensity score methods requires the identifying conditions of exchangeability,If L is sufficient to adjust for con-
founding and selection bias, then
π(L) is sufficient too. This result
was derived by Rosenbaum and Ru-
bin in a seminal paper published in
1983.
positivity, and consistency. The use of propensity score methods is justifed by
the following key result: Exchangeability of the treated and the untreated
within levels of the covariates L implies exchangeability within levels of the
propensity score π(L). That is, conditional exchangeability Y
a
⊥⊥A|L implies
Y
a
⊥⊥A|π(L). Further, positivity within levels of the propensity score π(L)—
which means that no individual has a propensity score equal to either 1 or
0—holds if and only if positivity within levels of the covariates L, as defined
in Chapter 2, holds.In a randomized experiment, the es-
timated π(L) adjusts for both sys-
tematic and random imbalances in
covariates, and thus does better
than adjustment for the true π(L)
which ignores random imbalances.
Under exchangeability and positivity within levels of the propensity score
π(L), the propensity score can be used to estimate causal effects using strat-
ification (including outcome regression), standardization, and matching. The
next two sections describe how to implement each of these methods. As a first
step, we must start by estimating the propensity score π(L) from the observa-
tional data and then proceeding to use the estimated propensity score in lieu
of the covariates L for stratification, standardization, or matching.
15.3 Propensity stratification and standardization
The average causal effect among individuals with a particular value s of the
propensity score π(L), i.e., E[Y
a=1,c=0
|π(L) = s] − E[Y
a=0,c=0
|π(L) = s] is
equal to E[Y |A = 1, C = 0, π(L) = s] −E[Y |A = 0, C = 0, π(L) = s] under the
identifying conditions. This conditional effect might be estimated by restrict-
Figure 15.2
ing the analysis to individuals with the value s of the true propensity score.
However, the propensity score π(L) is generally a continuous variable that can
take any value between 0 and 1. It is therefore unlikely that two individuals
will have exactly the same value s. For example, only individual 22005 had
an estimated π(L) of 0.6563, which means that we cannot estimate the causal
15.3 Propensity stratification and standardization 197
effect among individuals with π(L) = 0.6563 by comparing the treated and the
untreated with that particular value.
One approach to deal with the continuous propensity score is to create
strata that contain individuals with similar, but not identical, values of π(L).
The deciles of the estimated π(L) is a popular choice: individuals in the pop-
ulation are classified in 10 strata of approximately equal size, then the causal
effect is estimated in each of the strata. In our example, each decile containedcode: Program 15.3
approximately 162 individuals. The effect of smoking cessation on weight gain
ranged across deciles from 0.0 to 6.6 kg, but the 95% confidence intervals
around these point estimates were wide.
We could have also obtained these effect estimates by fitting an outcome
regression model for E[Y |A, C = 0, π(L)] that included as covariates treatment
A, 9 indicators for the deciles of the estimated π(L) (one of the deciles is the
reference level and is already incorporated in the intercept of the model), and
9 product terms between A and the indicators. Most applications of outcome
regression with deciles of the estimated π(L) do not include the product terms,
i.e., they assume no effect modification by π(L). In our example, a model
without product terms yields an effect estimate of 3.5 kg (95% confidence
interval: 2.6, 4.4). See Fine Point 15.2 for more on effect modification by the
propensity score.
Stratification on deciles or other functions of the propensity score raises a
potential problem: in general the distribution of the continuous π(L) will differ
between the treated and the untreated within some strata (e.g., deciles). If,
e.g., the average π(L) were greater in the treated than in the untreated in some
strata, then the treated and the untreated might not be exchangeable in those
strata. This problem did not arise in previous chapters, when we used func-
tions of the propensity score to estimate the parameters of structural models
via IP weighting and g-estimation, because those methods used the numericalCaution: the denominator of the
IP weights for a dichotomous treat-
ment A is not the propensity score
π(L), but a function of π(L). The
denominator is π(L) for the treated
(A = 1) and 1 − π(L) for the un-
treated (A = 0).
value of the estimated probability rather than a categorical transformation like
deciles. Similarly, the problem does not arise when using outcome regression
for E[Y |A, C = 0, π(L)] with the estimated propensity score π(L) as a contin-
uous covariate rather than as a set of indicators. When we used this latter
approach in our example the effect estimate was 3.6 (95% confidence interval:
2.7, 4.5) kg.
The validity of our inference depends on the correct specification of the
relationship between π(L) and the mean outcome Y (which we assumed to be
linear). However, because the propensity score is a one-dimensional summary
of the multi-dimensional L, it is easy to guard against misspecification of thisThough the propensity score is one-
dimensional, we still need to esti-
mate it from a model that regresses
treatment on a high-dimensional L.
The same applies to IP weighting
and g-estimation.
relationship by fitting flexible models cubic splines rather than a single linear
term for the propensity score. Note that IP weighting and g-estimation were
agnostic about the relationship between propensity score and outcome.
When our parametric assumptions for E[Y |A, C = 0, π(L)] are correct,
plus exchangeability and positivity hold, the model estimates the average
causal effects within all levels s of the propensity score E[Y
a=1,c=0
|π(L) =
s] −E[Y
a=0,c=0
|π(L) = s]. If we were interested in the average causal effect in
the entire study population E[Y
a=1,c=0
] − E[Y
a=0,c=0
], we would standardize
the conditional means E[Y |A, C = 0, π(L)] by using the distribution of the
propensity score. The procedure is the same one described in Chapter 13 forcode: Program 15.4
continuous variables, except that we replace the variables L by the estimated
π(L). Note that the procedure can naturally incorporate a product term be-
tween treatment A and the estimated π(L) in the outcome model. In our
example, the standardized effect estimate was 3.6 (95% confidence interval:
2.7, 4.6) kg.
198 Outcome regression and propensity scores
15.4 Propensity matching
The process of matching on the propensity score π(L) is analogous to match-
ing on a single continuous variable L, a procedure described in Chapter 4.
There are many forms of propensity matching. All of them attempt to form aAfter propensity matching, the
matched population has the π(L)
distribution of the treated, of the
untreated, or any other arbitrary
distribution.
matched population in which the treated and the untreated are exchangeable
because they have the same distribution of π(L). For example, one can match
the untreated to the treated: each treated individual is paired with one (or
more) untreated individuals with the same propensity score value. The subset
of the original population comprised by the treated-untreated pairs (or sets) is
the matched population. Under exchangeability and positivity given π(L), as-
sociation measures in the matched population are consistent estimates of effect
measures: the associational risk ratio in the matched population consistentlyA drawback of matching used to be
that nobody knew how to compute
the variance of the effect estimate.
That is no longer the case thanks
to the work of Abadie and Imbens
(2006).
estimates the causal risk ratio in the matched population.
Again, it is unlikely that two individuals will have exactly the same val-
ues of the propensity score π(L). In our example, propensity score matching
will be carried out by identifying, for each treated individual, one (or more)
untreated individuals with a close value of π(L). A common approach is to
match treated individuals with a value s of the estimated π(L) with untreated
individuals who have a value s ± 0.05, or some other small difference. For ex-
ample, treated individual 1089 (estimated π(L) of 0.6563) might be matched
with untreated individual 1088 (estimated π(L) of 0.6579). There are numer-
ous ways of defining closeness, and a detailed description of these definitions
is beyond the scope of this book.
Defining closeness in propensity matching entails a bias-variance trade-
off. If the closeness criteria are too loose, individuals with relatively different
values of π(L) will be matched to each other, the distribution of π(L) will
differ between the treated and the untreated in the matched population, and
exchangeability will not hold. On the other hand, if the closeness criteria are
too tight and many individuals are excluded by the matching procedure, there
will be approximate exchangeability but the effect estimate may have wider
95% confidence intervals.
The definition of closeness is also related to that of positivity. In our smok-
ing cessation example, the distributions of the estimated π(L) in the treatedRemember: positivity is now de-
fined within levels of the propensity
score, i.e., Pr [A = a|π(L) = s] >
0 for all s such that Pr [π(L) = s]
is nonzero.
and the untreated overlapped throughout most of the range (see Figure 15.1).
Only 2 treated individuals (0.01% of the study population) had values greater
than those of any untreated individual. When using outcome regression on the
estimated π(L) in the previous section, we effectively assumed that the lack
of untreated individuals with high π(L) estimates was due to chance—random
nonpositivity—and thus included all individuals in the analysis. In contrast,
most propensity matched analyses would not consider those two treated indi-
viduals close enough to any of the untreated individuals, and would exclude
them. Matching does not distinguish between random and structural nonpos-
itivity.
The above discussion illustrates how the matched population may be very
different from the target (super)population. In theory, propensity matching
can be used to estimate the causal effect in a well characterized target pop-
ulation. For example, when matching each treated individual with one or
more untreated individuals and excluding the unmatched untreated, one is es-
timating the effect in the treated (see Fine Point 15.2). In practice, however,
propensity matching may yield an effect estimate in a hard-to-describe subset
of the study population. For example, under a given definition of closeness,
some treated individuals cannot be matched with any untreated individuals
15.5 Propensity models, structural models, predictive models 199
and thus they are excluded from the analysis. As a result, the effect estimate
corresponds to a subset of the population that is defined by the values of the
estimated propensity score that have successful matches.
That propensity matching forces investigators to restrict the analysis to
treatment groups with overlapping distributions of the estimated propensity
score is often presented as a strength of the method. One surely would not want
to have biased estimates because of violations of positivity, right? However,
leaving aside issues related to random variability (see above), there is a price
to be paid for restrictions based on the propensity score. Suppose that, after
inspecting Figure 15.1, we conclude that we can only estimate the effect of
smoking cessation for individuals with an estimated propensity score less than
0.67. Who are these people? It is unclear because individuals do not come with
a propensity score tattooed on their forehead. Because the matched population
is not well characterized, it is hard to assess the transportability of the effect
estimate to other populations.
When positivity concerns arise, restriction based on real-world variablesEven if every subject came with
her propensity score tattooed on
her forehead, the population could
still be ill-characterized because the
same propensity score value may
mean different things in different
settings.
(e.g., age, number of cigarettes) leads to a more natural characterization of the
causal effect. In our smoking cessation example, the two treated individuals
with estimated π(L) > 0.67 were the only ones in the study who were over
age 50 and had smoked for less than 10 years. We could exclude them and
explain that our effect estimate only applies to smokers under age 50 and to
smokers 50 and over who had smoked for at least 10 years. This way of defining
the target population is more natural than defining it as those with estimated
π(L) < 0.67.
Using propensity scores to detect the overlapping range of the treated and
the untreated may be useful, but simply restricting the study population to
that range is a lazy way to ensure positivity. The automatic positivity ensured
by propensity matching needs to be weighed against the difficulty of assessing
transportability when restriction is solely based on the value of the estimated
propensity scores.
15.5 Propensity models, structural models, predictive models
In Part II of this book we have described two different types of models for causal
inference: propensity models and structural models. Let us now compare them.
Propensity models are models for the probability of treatment A given the
variables L that are used to achieve conditional exchangeability. We have
used propensity models for matching and stratification in this chapter, for IP
weighting in Chapter 12, and for g-estimation in Chapter 14. The parameters
of propensity models are nuisance parameters (see Fine Point 15.1) without a
causal interpretation because a variable L and treatment A may be associated
for many reasons—not only because the variable L causes A. For example, the
association between L and A can be interpreted as the effect of L on A under
Figure 7.1, but not under Figures 7.2 and 7.3. Yet propensity models are useful
for causal inference, often as the basis of the estimation of the parameters of
structural models, as we have described in this and previous chapters.
Structural models describe the relation between the treatment A and some
component of the distribution (e.g., the mean) of the counterfactual outcome
Y
a
, either marginally or within levels of the variables L. For continuous treat-
ments, a structural model is often referred to as a dose-response model. The
parameters for treatment in structural models are not nuisance parameters:
200 Outcome regression and propensity scores
Fine Point 15.2
Effect modification and the propensity score. A reason why matched and unmatched estimates may differ is effect
modification. As an example, consider the common setting in which the number of untreated individuals is much
larger than the number of treated individuals. Propensity matching often results in almost all treated individuals being
matched and many untreated individuals being unmatched and therefore excluded from the analysis. When this occurs,
the distribution of causal effect modifiers in the matched population will resemble that in the treated. Therefore, the
effect in the matched population will be closer to the effect in the treated than to the effect that would have been
estimated by methods that use data from the entire population. See Technical Point 4.1 for alternative ways to estimate
the effect of treatment in the treated via IP weighting and standardization.
Effect modification across propensity strata may be interpreted as evidence that decision makers know what they
are doing, e.g. that doctors tend to treat patients who are more likely to benefit from treatment (Kurth et al 2006).
However, the presence of effect modification by π(L) may complicate the interpretation of the estimates. Consider a
situation with qualitative effect modification: “Doctor, according to our study, this drug is beneficial for patients who
have a propensity score between 0.11 and 0.93 when they arrive at your office, but it may kill those with propensity
scores below 0.11,” or “Ms. Minister, let’s apply this educational intervention to children with propensity scores below
0.57 only.” The above statements are of little policy relevance because, as discussed in the main text, they are not
expressed in terms of the measured variables L.
Finally, besides effect modification, there are other reasons why matched estimates may differ from the overall effect
estimate: violations of positivity in the non-matched, an unmeasured confounder that is more/less prevalent (or that is
better/worse measured) in the matched population than in the unmatched population, etc. As discussed for individual
variables L in Chapter 4, apparent effect modification might be explained by differences in residual confounding across
propensity strata.
they have a direct causal interpretation as outcome differences under differ-
ent treatment values a. We have described two classes of structural models:
marginal structural models and structural nested models. Marginal structural
models include parameters for treatment, for the variables V that may be ef-
fect modifiers, and for product terms between treatment and variables V . The
choice of V reflects only the investigator’s substantive interest in effect mod-
ification (see Section 12.5). If no covariates V are included, then the model
is truly marginal. If all variables L are included as possible effect modifiers,
then the marginal structural model becomes a faux marginal structural model.See Fine Point 14.1 for a discussion
of the relation between structural
nested models and faux semipara-
metric marginal structural models,
and other subtleties.
Structural nested models include parameters for treatment and for product
terms between treatment A and all variables in L that are effect modifiers.
We have presented outcome regression as a method to estimate the param-
eters of faux marginal structural models for causal inference. However, out-
come regression is also widely used for purely predictive, as opposed to causal,
purposes. For example, online retailers use sophisticated outcome regression
models to predict which customers are more likely to purchase their products.
The goal is not to determine whether your age, sex, income, geographic origin,
and previous purchases have a causal effect on your current purchase. Rather,A study found that Facebook Likes
predict sexual orientation, politi-
cal views, and personality traits
(Kosinski et al, 2013). This is
purely predictive, not necessarily
causal.
the goal is to identify those customers who are more likely to make a purchase
so that specific marketing programs can be targeted to them. It is all about
association, not causation. Similarly, doctors use algorithms based on outcome
regression to identify patients at high risk of developing a serious disease or
dying. The parameters of these predictive models do not necessarily have any
causal interpretation and all covariates in the model have the same status, i.e.,
there are no treatment variable A and variables L.
The dual use of outcome regression in both causal inference method and
15.5 Propensity models, structural models, predictive models 201
in prediction has led to many misunderstandings. One of the most important
misunderstandings has to do with variable selection procedures. When the in-
terest lies exclusively on outcome prediction, investigators may want to select
any variables that, when included as covariates in the model, improve its pre-
dictive ability. Many well-known variable selection procedures—e.g., forward
selection, backward elimination, stepwise selection—and more recent develop-
ments in machine learning are used to enhance prediction. These are powerful
tools for investigators who are interested in prediction, especially when dealing
with very high-dimensional data.
Unfortunately, statistics courses and textbooks have not always made a
sharp difference between causal inference and prediction. As a result, these
variable selection procedures for predictive models have often been applied to
causal inference models. A possible result of this mismatch is the inclusion of
superfluous—or even harmful—covariates in propensity models and structural
models. Specifically, the application of predictive algorithms to causal inference
models may result in inflated variances and greater bias.
The problem arises because of the widespread, but mistaken, belief that
propensity models should predict treatment A as well as possible. PropensityIt is not uncommon for propen-
sity analyses to report measures of
predictive power like Mallows’s Cp.
The relevance of these measures for
causal inference is questionable.
models do not need to predict treatment very well. They just need to include
the variables L that guarantee exchangeability. Covariates that are strongly
associated with treatment, but are not necessary to guarantee exchangeability,
do not help reduce bias. If these covariates were included in L, adjustment can
result in estimates with very large variances, or even amplify existing bias.
Consider the following example. Suppose all individuals in a certain study
attend either hospital Aceso or hospital Panacea. Doctors in hospital Aceso
give treatment A = 1 to 99% of the individuals, and those in hospital Panacea
give A = 0 to 99% of the individuals. Suppose the variable Hospital has
no effect on the outcome (except through its effect on treatment A) and is
therefore not necessary to achieve conditional exchangeability. Say we decide
to add Hospital as a covariate in our propensity model anyway. The propensity
score π(L) in the target population is about 0.99 for individuals in hospital
Aceso and 0.01 for those in hospital Panacea, but by chance we may end up
with a study population in which everybody in hospital Aceso has A = 1 or
everybody in hospital Panacea has A = 0 for some strata defined by L. ThatIf we perfectly predicted treatment,
then all treated individuals would
have π(L) = 1 and all untreated
individuals would have π(L) = 0.
There would be no overlap and the
analysis would be impossible.
is, our effect estimate may have a near-infinite variance without any reduction
in confounding. That treatment is now very well predicted is irrelevant for
causal inference purposes.
Besides variance inflation, a predictive attitude towards variable selection
for causal inference models—both propensity models and outcome regression
models—may also result in self-inflicted bias. For example, the inclusion of
colliders as covariates may result in systematic bias even if colliders may be
effective covariates for purely predictive purposes, and the inclusion of instru-
ments (see next chapter) may amplify bias due to unmeasured variables. We
will return to these issues in Chapter 18.
In general, causal inference methods based on models—propensity models
and structural models—require no misspecification of the functional form for
the covariates. To reduce the possibility of model misspecification, we use flex-
ible specifications cubic splines rather than linear terms. In addition, these
causal inference methods require the conditions of exchangeability, positivity,
and well-defined interventions for unbiased causal inferences. In the next chap-
ter we describe a very different type of causal inference method that does not
require exchangeability of treatment.
202 Outcome regression and propensity scores
Chapter 16
INSTRUMENTAL VARIABLE ESTIMATION
The causal inference methods described so far in this book rely on a key untestable assumption: all variables needed
to adjust for confounding and selection bias have been identified and correctly measured. If this assumption is
incorrect—and it will always be to a certain extent—there will be residual bias in our causal estimates.
It turns out that there exist other methods that can validly estimate causal effects under an alternative set
of assumptions that do not require measuring all adjustment factors. Instrumental variable estimation is one of
those methods. Economists and other social scientists reading this book can breathe now. We are finally going to
describe a very common method in their fields, a method that is unlike any other we have discussed so far.
16.1 The three instrumental conditions
The causal diagram in Figure 16.1 depicts a randomized trial: Z is the ran-
domization assignment indicator (1: treatment, 0: placebo), A is an indicator
for receiving treatment (1: yes, 0: no) because not all participants adhere to
their assignment, Y the outcome, and U all factors (some unmeasured) that
affect both the outcome and the adherence. Because participants and their
doctors do not know whether the pill they are given is treatment or placebo,
they are said to be “blinded ” and the study is referred to as a double-blind
placebo-controlled randomized trial.
Suppose we want to consistently estimate the average causal effect of A on
Y . Whether we use IP weighting, standardization, g-estimation, stratification,
or matching, we need to correctly measure, and adjust for, variables that block
the backdoor path A ← U → Y , i.e., we need to ensure conditional exchange-
Figure 16.1
Figure 16.2
ability of the treated and the untreated. Unfortunately, all these methods will
result in biased effect estimates if some of the necessary variables are unmea-
sured, imperfectly measured, or misspecified in the model.
Instrumental variable (IV) methods are different: they may be used to
attempt to identify the average causal effect of A on Y in this randomized
trial, even if we did not measure the variables normally required to adjust
for the confounding caused by U. To perform their magic, IV methods need
an instrumental variable Z, or an instrument. A variable Z is an instrument
because it meets three instrumental conditions:
(i) Z is associated with A
(ii) Z does not affect Y except through its potential effect on A
(iii) Z and Y do not share causes
See Technical Point 16.1 for a more rigorous definition of these conditions,
which we will use in the other technical points.
In the double-blind randomized trial described above, the randomizationCondition (ii) would not be guar-
anteed if, for example, partici-
pants were inadvertently unblinded
by side effects of treatment.
indicator Z is an instrument. Condition (i) is met because trial participants are
more likely to receive treatment if they were assigned to treatment, condition
(ii) is expected by the double-blind design, and condition (iii) is expected by
the random assignment of Z.
204 Instrumental variable estimation
Technical Point 16.1
The instrumental conditions, formally. Instrumental condition (i), sometimes referred to as the relevance condition,
is non-null association between Z and A, or Z⊥⊥A does not hold. Condition (i) is expected to hold in randomized
experiments because treatment assignment is expected to influence the treatment received.
Instrumental condition (ii), commonly known as the exclusion restriction, is the condition of “no direct effect of Z
on Y .” At the individual level, condition (ii) is Y
z,a
i
= Y
z
′
,a
i
= Y
a
i
for all z, z
′
, all a, all individuals i. However, for
some results presented in this chapter, only the population level condition (ii) is needed, i.e., E [Y
z,a
] = E
h
Y
z
′
,a
i
.
Both versions of condition (ii) are expected to hold in double-blind randomized experiments because assignment is
not expected to influence the outcome (e.g., through behavioral changes) if assignment is unknown to all individuals.
Condition (ii) is trivially true for surrogate instruments.
Instrumental condition (iii) can be written as marginal exchangeability Y
a,z
⊥⊥Z for all a, z, which holds in the SWIGs
corresponding to Figures 16.1, 16.2, and 16.3. Together with condition (ii) at the individual level, it implies Y
a
⊥⊥Z.
A stronger condition (iii) is joint exchangeability, or {Y
z,a
; a ∈ [0, 1], z ∈ [0, 1]}⊥⊥Z for dichotomous treatment and
instrument. See Technical Point 2.1 for a discussion on different types of exchangeability and Technical Point 16.2 for
a description of results that require each version of exchangeability. Both versions of condition (iii) are expected to hold
in randomized experiments because Z is randomly assigned.
Figure 16.1 depicts a special case in which the instrument Z has a causal ef-
fect on the treatment A. We then refer to Z as a causal instrument. Sometimes
the causal instrument is unmeasured and we use a measured proxy or surrogate
instrument Z that is associated with the unmeasured causal instrument U
Z
. A
surrogate instrument does not have a causal effect on treatment A, but meets
the instrumental conditions with the Z-A association (i) now resulting from
the cause U
Z
shared by Z and A, and with condition (iii) modified as “Z and
Y do not share causes except for U
Z
”. Both causal and surrogate instruments
can be used for IV estimation, with some caveats described in Section 16.4. As
Figure 16.3
a curiosity, Figure 16.3 depicts an example of an unusual surrogate instrument
Z in a selected population: the Z-A association arises from conditioning on a
common effect S of the unmeasured causal instrument U
Z
and the surrogate
instrument Z.
In previous chapters we have estimated the effect of smoking cessation on
weight change using various causal inference methods applied to observational
data. To estimate this effect using IV methods, we need an instrument Z.
Since there is no randomization indicator in an observational study, consider
the following candidate for an instrument: the price of cigarettes. It can
be argued that this variable meets the three instrumental conditions if (i)
cigarette price affects the decision to quit smoking, (ii) cigarette price affects
weight change only through its effect on smoking cessation, and (iii) no common
causes of cigarette price and weight change exist. Fine Point 16.1 reviews some
proposed instruments in observational studies.
To fix ideas, let us propose an instrument Z that takes value 1 when the
average price of a pack of cigarettes in the U.S. state where the individual wasCondition (i) is met if the candi-
date instrument Z “price in state
of birth” is associated with smok-
ing cessation A through the unmea-
sured variable U
Z
“price in place of
residence”.
born was greater than $1.50, and takes value 0 otherwise. Unfortunately, we
cannot determine whether our variable Z is actually an instrument. Of the
three instrumental conditions, only condition (i) is empirically verifiable. To
verify this condition we need to confirm that the proposed instrument Z and the
treatment A are associated, i.e., that Pr [A = 1|Z = 1] − Pr [A = 1|Z = 0] >
0. The probability of quitting smoking is 25.8% among those with Z = 1
and 19.5% among those with Z = 0; the risk difference Pr [A = 1|Z = 1] −
16.1 The three instrumental conditions 205
Fine Point 16.1
Candidate instruments in observational studies. Many variables have been proposed as instruments in observational
studies and it is not possible to review all of them here. Three commonly used categories of candidate instruments are
• Genetic factors: The proposed instrument is a genetic variant Z that is associated with treatment A and that,
supposedly, is only related with the outcome Y through A. For example, when estimating the effects of alcohol
intake on the risk of coronary heart disease, Z can be a polymorphism associated with alcohol metabolism (say,
ALDH2 in Asian populations). Causal inference from observational data via IV estimation using genetic variants is
part of the framework known as Mendelian randomization (Katan 1986, Davey Smith and Ebrahim 2004, Didelez
and Sheehan 2007, VanderWeele et al. 2014).
• Preference: The proposed instrument Z is a measure of the physician’s (or a care provider’s) preference for one
treatment over the other. The idea is that a physician’s preference influences the prescribed treatment A without
having a direct effect on the outcome Y . For example, when estimating the effect of prescribing COX-2 selective
versus non-selective nonsteroidal anti-inflammatory drugs on gastrointestinal bleeding, U
Z
can be the physician’s
prescribing preference for drug class (COX-2 selective or non-selective). Because U
Z
is unmeasured, investigators
replace it in the analysis by a (measured) surrogate instrument Z, such as “last prescription issued by the physician
before current prescription” (Korn and Baumrind 1998, Earle et al. 2001, Brookhart and Schneeweiss 2007).
• Access: The proposed instrument Z is a measure of access to the treatment. The idea is that access impacts the
use of treatment A but does not directly affect the outcome Y . For example, physical distance or travel time to
a facility has been proposed as an instrument for treatments available at such facilities (McClellan et al. 1994,
Card 1995, Baiocchi et al. 2010). Another example: calendar period has been proposed as an instrument for a
treatment whose accessibility varies over time (Hoover et al. 1994, Detels et al. 1998). In the main text we use
“price of the treatment”, another measure of access, as a candidate instrument.
Pr [A = 1|Z = 0] is therefore 6%. When, as in this case, Z and A are weakly
associated, Z is often referred as a weak instrument (more on weak instruments
in Section 16.5).
On the other hand, conditions (ii) and (iii) cannot be empirically verified.
To verify condition (ii), we would need to prove that Z can only cause the
outcome Y through the treatment A. We cannot prove it by conditioning
on A, which is a collider on the pathway Z ←− U
Z
→ A ←− U → Y in
Figure 16.2, because that would induce an association between Z and Y even
if condition (ii) held true. And we cannot, of course, prove that condition (iii)
holds because we can never rule out confounding for the effect of any variable.
We can only assume that conditions (ii) and (iii) hold. IV estimation, like allConditions (ii) and (iii) can some-
times be empirically falsified by us-
ing data on instrument, treatment,
and outcome. However, falsifica-
tion tests only reject the conditions
for a small subset of violations. For
most violations, the test has no sta-
tistical power, even for an arbitrarily
large sample size (Balke and Pearl
1997, Bonet 2001, Glymour et al.
2012).
methods we have studied so far, is based on untestable assumptions.
In observational studies we cannot prove that our proposed instrument Z
is truly an instrument. We refer to Z as a proposed or candidate instrument
because we can never guarantee that the structures represented in Figures
16.1 and 16.2 are the ones that actually occur. The best we can do is to use
subject-matter knowledge to build a case for why the proposed instrument Z
may be reasonably assumed to meet conditions (ii) and (iii); this is similar to
how we use subject-matter knowledge to justify the identifying assumptions of
the methods described in previous chapters.
But let us provisionally assume that Z is an instrument. Now what? Can
we now see the magic of IV estimation in action? Can we consistently estimate
the average causal effect of A on Y without having to identify and measure
206 Instrumental variable estimation
Technical Point 16.2
Bounds: Partial identification of causal effects. For a dichotomous outcome Y , the average causal effect
Pr
Y
a=1
= 1
− Pr
Y
a=0
= 1
can take values between −1 (if all individuals develop the outcome unless they were
treated) and 1 (if no individuals develop the outcome unless treated). The bounds of the average causal effect are
(−1, 1). The distance between these bounds can be cut in half by using the data: because for each individual we know
the value of either her counterfactual outcome Y
a=1
(if the individual was actually treated) or Y
a=0
(if the individual
was actually untreated), we can compute the causal effect after assigning the most extreme values possible to each
individual’s unknown counterfactual outcome. This will result in bounds of the average causal effect that are narrower
but still include the null value 0. For a continuous outcome Y , deriving bounds requires the specification of the minimum
and maximum values for the outcome; the width of the bounds will vary depending on the chosen values.
The bounds for Pr
Y
a=1
= 1
−Pr
Y
a=0
= 1
can be further narrowed if there is a variable Z that meets instrumental
condition (ii) at the population level (see Technical Point 16.1) and marginal exchangeability (iii) (Robins 1989; Manski
1990). The width of these so-called natural bounds, Pr[A = 1|Z = 0] + Pr[A = 0|Z = 1], is narrower than that of
the bounds identified from the data alone. Sometimes narrower bounds—the so-called sharp bounds—can be achieved
when marginal exchangeability is replaced by joint exchangeability (Balke and Pearl 1997; Richardson and Robins 2014).
The conditions necessary to achieve the sharp bounds can also be derived from the SWIGs under joint interventions
on z and a corresponding to any of the causal diagrams depicted in Figures 16.1, 16.2, and 16.3. Richardson and Robins
(2010, 2014) showed that the conditions Y
a,z
⊥⊥(Z, A) |U and Z⊥⊥U, together with a population level condition (ii)
within levels of U, i.e., E [Y
z,a
|U] = E
h
Y
z
′
,a
|U
i
, are sufficient to obtain the sharp bounds. These conditions, which hold
for all three SWIGs, imply Z⊥⊥U, Y ⊥⊥Z|U, A, and that E [Y
z,a
] is given by the g-formula
R
E [Y |A = a, U = u] dF (u)
ignoring Z, which reflects that Z has no direct effect on Y within levels of U . Dawid (2003) proved that these latter
conditions lead to the sharp bounds. Under further assumptions, Richardson and Robins derived yet narrower bounds.
See also Richardson, Evans, and Robins (2011).
Unfortunately, all these partial identification methods (i.e., methods for bounding the effect) are often relatively
uninformative because the bounds are wide. Swanson et al (2018) review partial identification methods for binary
instruments, treatments, and outcomes. Swanson et al. (2015a) describe a real-world application of several partial
identification methods and discuss their relative advantages and disadvantages.
There is a way to decrease the width of the bounds: making parametric assumptions about the form of the effect of
A on Y . Under sufficiently strong assumptions described in Section 16.2, the upper and lower bounds converge into a
single number and the average causal effect is point identified.
the confounders? Sadly, the answer is no without further assumptions. An
instrument by itself does not allow us to identify the average causal effect of
smoking cessation A on weight change Y , but only identifies certain upper and
lower bounds. Typically, the bounds are very wide and often include the null
value (see Technical Point 16.2).
In our example, these bounds are not very helpful. They would only confirm
what we already knew: smoking cessation can result in weight gain, weight loss,
or no weight change. Unfortunately, that is all an instrument can offer unless
one is willing to make additional unverifiable assumptions. Sections 16.3 and
16.4 review additional conditions under which the IV estimand is the average
causal effect. Before that, we review the methods to do so.
16.2 The usual IV estimand
When a dichotomous variable Z is an instrument, i.e., meets the three instru-
mental conditions (i)-(iii), and an additional condition (iv) described in the
16.2 The usual IV estimand 207
next section holds, then the average causal effect of treatment on the additive
scale E
Y
a=1
− E
Y
a=0
is identified and equalsWe will focus on dichotomous in-
struments, which are the common-
est ones. For a continuous instru-
ment Z, the usual IV estimand is
Cov(Y,Z)
Cov(A,Z)
, where Cov means covari-
ance.
E [Y |Z = 1] − E [Y |Z = 0]
E [A|Z = 1] − E [A|Z = 0]
,
which is the usual IV estimand for a dichotomous instrument. (Note E [A|Z = 1] =
Pr [A = 1|Z = 1] for a dichotomous treatment). Technical Point 16.3 provides
a proof of this result in terms of an additive structural mean model, but you
might want to wait until the next section before reading it.
To intuitively understand the usual IV estimand, consider again the ran-
domized trial from the previous section. The numerator of the IV estimand isIn randomized experiments, the IV
estimand is the ratio of two effects
of Z: the effect of Z on Y and the
effect of Z on A. Each of these ef-
fects can be consistently estimated
without adjustment because Z is
randomly assigned.
the average causal effect of assignment Z on Y —the intention-to-treat effect—
and the denominator is the average causal effect of assignment Z on A—a
measure of adherence to, or compliance with, the assigned treatment. When
there is perfect adherence, the denominator is equal to 1, and the effect of A on
Y equals the effect of Z on Y . As adherence worsens, the denominator starts
to get closer to 0, and the effect of A on Y becomes greater than the effect of
Z on Y . The lower the adherence, the greater the difference between the effect
of A on Y —the IV estimand—and the effect of Z on Y .
The IV estimand bypasses the need to adjust for the confounders by inflat-
ing the effect of assignment (the numerator). The magnitude of the inflation
increases as adherence decreases, i.e., as the Z-A risk difference (the denomi-
nator) gets closer to zero. The same rationale applies to the instruments used
in observational studies, where the denominator of the IV estimator may equal
either the causal effect of the causal instrument Z on A (Figure 16.1), or the
noncausal association between the surrogate instrument Z and the treatment
A (Figures 16.2 and 16.3).
The standard IV estimator is the ratio of the estimates of the numeratorAlso known as the Wald estimator
(Wald 1940). and the denominator of the usual IV estimand. In our smoking cessation
example with a dichotomous instrument Z (1: state with high cigarette price,
0: otherwise), the numerator estimate
b
E [Y |Z = 1]−
b
E [Y |Z = 0] equals 2.686−
2.536 = 0.1503 and the denominator
b
E [A|Z = 1] −
b
E [A|Z = 0] equals 0.2578 −
0.1951 = 0.0627. Therefore, the usual IV estimate is the ratio 0.1503/0.0627 =Code: Program 16.1
For simplicity, we exclude individu-
als with missing outcome or instru-
ment. In practice, we could use IP
weighting to adjust for possible se-
lection bias before using IV estima-
tion.
2.4 kg. Under the three instrumental conditions (i)-(iii) plus condition (iv)
from next section, this is an estimate of the average causal effect of smoking
cessation on weight gain in the population.
We estimated the numerator and denominator of the IV estimand by simply
calculating the four sample averages
b
E [A|Z = 1],
b
E [A|Z = 0],
b
E [Y |Z = 1], and
b
E [Y |Z = 0]. Equivalently, we could have fit two (saturated) linear models to
estimate the differences in the denominator and the numerator. The model
for the denominator would be E [A|Z] = α
0
+ α
1
Z, and the model for the
numerator E [Y |Z] = β
0
+ β
1
Z.
An alternative method to calculate the standard IV estimator is the two-
stage-least-squares estimator. The procedure is as follows. First, fit the first-
stage treatment model E [A|Z] = α
0
+ α
1
Z, and generate the predicted val-
ues
b
E [A|Z] for each individual. Second, fit the second-stage outcome model
E [Y |Z] = β
0
+ β
1
b
E [A|Z]. The parameter estimate
b
β
1
will always be nu-
merically equivalent to the standard IV estimate. Thus, in our example, theCode: Program 16.2
two-stage-least-squares estimate was again 2.4 kg.
The 2.4 point estimate has a very large 95% confidence interval: −36.5 to
41.3. This is expected for our proposed instrument because the Z-A association
is weak and there is much uncertainty in the first-stage model. A commonly
208 Instrumental variable estimation
used rule of thumb is to declare an instrument as weak if the F-statistic from
the first-stage model is less than 10 (it was a meager 0.8 in our example). We
will revisit the problems raised by weak instruments in Section 16.5.
Some of the assumptions implicit in regarding the two-stage-least-squares
estimator as identifying the causal effect of treatment can be made more ex-
plicit by using additive or multiplicative structural mean models, like the ones
described in Technical Points 16.3 and 16.4, for IV estimation. The parameters
of structural mean models can be estimated via g-estimation. In addition, inCode: Program 16.3
the presence of measured common causes L of the instrument and the outcome
that therefore must be adjusted for in the analysis, the trade-offs involved in
the choice between two-stage-least-squares linear models and structural mean
models can be similar to those involved in the choice between outcome regres-
sion and structural nested models for non-IV estimation (see Chapters 14 and
15).
Anyway, the above estimators are only valid when the usual IV estimand
can be interpreted as the average causal effect of treatment A on the outcome
Y . For that to be true, a fourth identifying condition needs to hold in addition
to the three instrumental conditions.
16.3 A fourth identifying condition: homogeneity
The three instrumental conditions (i)-(iii) are insufficient to ensure that the IV
estimand is the average causal effect of treatment A on Y . A fourth condition,
effect homogeneity (iv), is needed. Here we describe four possible homogeneity
conditions (iv) in order of (historical) appearance.
The most extreme, and oldest, version of homogeneity condition (iv) is
constant effect of treatment A on outcome Y across individuals. In our ex-
ample, this condition would hold if smoking cessation made every individual
in the population gain (or lose) the same amount of weight, say, exactly 2.4
kg. A constant effect is equivalent to additive rank preservation which, as we
discussed in Section 14.4, is scientifically implausible for most treatments and
outcomes—and impossible for dichotomous outcomes, except under the sharpYet additive rank preservation was
implicitly assumed in many early IV
analyses using the two-stage-least-
squares estimator.
null or universal harm (or benefit). In our example, we expect that, after quit-
ting smoking, some individuals will gain a lot of weight, some will gain little,
and others may even lose some weight. Therefore, we are not generally will-
ing to accept the homogeneity assumption of constant effect as a reasonable
condition (iv).
A second, less extreme homogeneity condition (iv) for dichotomous Z and
A is equality of the average causal effect of A on Y across levels of Z in
both the treated and in the untreated, i.e., E
Y
a=1
− Y
a=0
|Z = 1, A = a
=
E
Y
a=1
− Y
a=0
|Z = 0, A = a
for a = 0, 1. This additive homogeneity condi-Even when condition (iii) Y
a
⊥⊥Z
holds—as in the SWIGs for Figures
16.1, 16.2, 16.3—Y
a
⊥⊥Z|A does
not generally hold. Therefore the
treatment effect may depend on Z,
i.e., the less extreme homogeneity
condition may not hold.
tion (iv) was the one used in the mathematical proof of Technical Point 16.3.
An alternative homogeneity condition on the multiplicative scale is discussed
in Technical Point 16.4. (This multiplicative homogeneity condition leads to
an IV estimand that is different from the usual IV estimand.)
The above homogeneity condition is expressed in terms that are not natu-
rally intuitive. How can subject-matter experts provide arguments in support
of a constant average causal effect within levels of the proposed instrument
Z and the treatment A in any particular study? More natural—even if still
untestable—homogeneity conditions (iv) would be stated in terms of effect
modification by possibly known (even if unmeasured) confounders U . One
16.3 A fourth identifying condition: homogeneity 209
Technical Point 16.3
Additive structural mean models and IV estimation. Consider the following saturated, additive structural mean
model for a dichotomous treatment A and an instrument Z as depicted in Figures 16.1, 16.2, or 16.3:
E
Y
a=1
− Y
a=0
|A = 1, Z
= β
0
+ β
1
Z
This model can also be written as E
Y − Y
a=0
|A, Z
= A (β
0
+ β
1
Z). The parameter β
0
is the average causal effect
of treatment among the treated individuals with Z = 0, and β
0
+ β
1
is the average causal effect of treatment among
the treated individuals with Z = 1. Thus β
1
quantifies additive effect modification by Z.
If we a priori assume that there is no additive effect modification by Z, then β
1
= 0 and β
0
is exactly the usual IV
estimand (Robins 1994). That is, the usual IV estimand is the parameter of an additive structural mean model for the
effect of treatment on the treated under no effect modification by Z.
The proof is simple. When Z is an instrument, condition (ii) holds, which implies E
Y
a=0
|Z = 1
= E
Y
a=0
|Z = 0
.
Under the above structural model, this conditional mean independence can be rewritten as E [Y − A (β
0
+ β
1
) |Z = 1] =
E [Y − Aβ
0
|Z = 0]. Solving the above equation with β
1
= 0 we have
β
0
=
E [Y |Z = 1] − E [Y |Z = 0]
E [A|Z = 1] − E [A|Z = 0]
You may wonder why we a priori set β
1
= 0. The reason is that we have an equation with two unknowns (β
0
and β
1
)
and that equation exhausts the constraints on the data distribution implied by the three instrumental conditions. Since
we need an additional constraint, which by definition will be untestable, we arbitrarily choose β
1
= 0 (rather than, say,
β
1
= 2). This is what we mean when we say that an instrument is insufficient to identify the average causal effect.
Therefore, to conclude that the average causal effect of treatment in the treated β
0
=
E
Y
a=1
− Y
a=0
|A = 1, Z = z
= E
Y
a=1
− Y
a=0
|A = 1
equals the average causal effect in the study popu-
lation E
Y
a=1
−E
Y
a=0
—and thus that the usual IV estimand is E
Y
a=1
−E
Y
a=0
—we must assume that the
effects of treatment in the treated and in the untreated are identical, which is an additional untestable assumption.
Hence, under the additional assumption β
1
= 0, β
0
= E
Y
a=1
− Y
a=0
|A = 1, Z = z
= E
Y
a=1
− Y
a=0
|A = 1
for any z is the average causal effect of treatment in the treated.
To conclude that β
0
is the average causal effect in the study population E
Y
a=1
− E
Y
a=0
—and thus that
E
Y
a=1
− E
Y
a=0
is the usual IV estimand—we must assume that the effects of treatment are identical in the
treated and in the untreated, i.e., the parameter for Z is also 0 in the structural model for A = 0. This is an additional
untestable assumption.
such condition is that U is not an additive effect modifier, i.e., that the av-
erage causal effect of A on Y is the same at every level of the unmeasured
confounder U or E
Y
a=1
|U
−E
Y
a=0
|U
= E
Y
a=1
−E
Y
a=0
. This thirdHern´an and Robins (2006b) showed
that, if U is an additive effect mod-
ifier, then it would not be reason-
able for us to believe that the previ-
ous additive homogeneity condition
(iv) holds.
homogeneity condition (iv) is often implausible because some unmeasured con-
founders may also be effect modifiers. For example, the magnitude of weight
gain after smoking cessation may vary with prior intensity of smoking, which
may itself be an unmeasured confounder for the effect of smoking cessation on
weight gain.
Another type of homogeneity condition (iv) is that the Z-A association on
the additive scale is constant across levels of the unmeasured confounders U,
i.e., E [A|Z = 1, U ] − E [A|Z = 0, U] = E [A|Z = 1] − E [A|Z = 0]. Both thisWang and Tchetgen Tchetgen
(2018) proposed the homogeneity
condition “t(U) is a constant” and
proved that it was a special case of
the general condition. See a proof
in Technical Point 16.5
condition and the earlier condition E
Y
a=1
|U
− E
Y
a=0
|U
= E
Y
a=1
−
E
Y
a=0
are special cases of the following (much more) general condition:
the modification by U of the effect of the treatment A on the outcome Y ,
e (U) ≡ E
Y
a=1
− Y
a=0
|U
, is uncorrelated with the modification by U of the
Z-A association on the additive scale, t (U) ≡ E [A|Z = 1, U ] −E [A|Z = 0, U],
210 Instrumental variable estimation
Technical Point 16.4
Multiplicative structural mean models and IV estimation. Consider the following saturated, multiplicative (log-
linear) structural mean model for a dichotomous treatment A
E
Y
a=1
|A = 1, Z
E [Y
a=0
|A = 1, Z]
= exp (β
0
+ β
1
Z) ,
which can also be written as E [Y |A, Z] = E
Y
a=0
|A, Z
exp [A (β
0
+ β
1
Z)]. For a dichotomous Y , exp (β
0
) is the
causal risk ratio in the treated individuals with Z = 0 and exp (β
0
+ β
1
) is the causal risk ratio in the treated with
Z = 1. Thus β
1
quantifies multiplicative effect modification by Z. If we a priori assume that β
1
= 0—and additionally
assume no multiplicative effect modification by Z in the untreated—then the causal effect on the multiplicative (risk
ratio) scale is E
Y
a=1
/ E
Y
a=0
= exp (β
0
), and the causal effect on the additive (risk difference) scale is
E
Y
a=1
− E
Y
a=0
= E [Y |A = 0] (1 − E [A]) [exp (β
0
) − 1] + E [Y |A = 1] E [A] [1 − exp (−β
0
)]
The proof, which relies on the instrumental conditions, can be found in Robins (1989) and Hern´an and Robins (2006b).
That is, if we assume a multiplicative structural mean model with no multiplicative effect modification by Z in the
treated and in the untreated, then the average causal effect E
Y
a=1
− E
Y
a=0
remains identified, but no longer
equals the usual IV estimator. As a consequence, our estimate of E
Y
a=1
− E
Y
a=0
will depend on whether we
assume no additive or multiplicative effect modification by Z. Unfortunately, it is not possible to determine which, if
either, assumption is true even if we had an infinite sample size (Robins 1994) because, when considering saturated
additive or multiplicative structural mean models, we have more unknown parameters to estimate than equations to
estimate them with. That is precisely why we need to make modeling assumptions such as homogeneity.
i.e., Cov [e (U) , t (U)] = 0. The previous two conditions are special cases of
Cov [e (U) , t (U)] = 0 because they can be expressed as “e(U) is a constant”and
“t(U) is a constant”, respectively, and the covariance of any variable with a
constant is always 0.
Because of the perceived implausibility of the homogeneity conditions in
many settings, the possibility that IV methods can validly estimate the average
causal effect of treatment seems questionable. There are two approaches that
bypass the homogeneity conditions.
One approach is the introduction of baseline covariates in the models for IV
estimation. To do so, it is safer to use structural mean models, which impose
fewer parametric assumptions than two-stage-linear-squares estimators. The
inclusion of covariates in a structural mean model allows the treatment effect
in the treated to vary with Z by imposing constraints on how the treatmentAlso, models can be used to in-
corporate multiple proposed in-
struments simultaneously, to han-
dle continuous treatments, and to
estimate causal risk ratios when
the outcome is dichotomous (see
Palmer et al. 2011 for a review).
effect varies within levels of the covariates. See Section 16.5. and Technical
Point 16.6 for more details on structural mean models with covariates.
Another approach is to use an alternative condition (iv) that does not
require effect homogeneity. When combined with the three instrumental con-
ditions (i)-(iii), this alternative condition allows us to endow the usual IV
estimand with a causal interpretation, even though it does not suffice to iden-
tify the average causal effect in the population. We review this alternative
condition (iv) in the next section.
16.4 An alternative fourth condition: monotonicity 211
Technical Point 16.5
Proof of the general homogeneity condition. We wish to show that E[Y
a=1
− Y
a=0
] =
E[Y |Z=1]−E[Y |Z=0]
E[A|Z=1]−E[A|Z=0]
under
the causal diagram in Figure 16.1 and the general homogeneity condition of zero covariance Cov (e (U) , t (U)) = 0,
where e (U) and t (U) are defined in the main text.
To do so, note that E [e (U)] = E[Y
a=1
− Y
a=0
]. Further, E [t (U)] = E [A|Z = 1] − E [A|Z = 0] because U⊥⊥Z.
Hence the zero covariance condition implies E[e (U) t (U)]/ {E [A|Z = 1] − E [A|Z = 0]} = E[Y
a=1
−Y
a=0
]. It remains
to show that E [Y |Z = 1] − E [Y |Z = 0] = E[e (U) t (U)]. To do so, write Y = A
Y
a=1
− Y
a=0
+ Y
a=0
. Because
Y
a
⊥⊥(A, Z) |U and U⊥⊥Z in Figure 16.1, we have E [Y |Z] equal to
=
P
u
P
a={0,1}
E [Y |A = a, Z, U = u] Pr (A = a|Z, U = u) f (u|Z)
=
P
u
E[Y
a=1
− Y
a=0
|U = u] Pr (A = 1|Z, U = u) + E
Y
a=0
|U = u
f (u).
Thus, E [Y |Z = 1] −E [Y |Z = 0] = E
E[Y
a=1
− Y
a=0
|U]
{Pr (A = 1|Z = 1, U) − Pr (A = 1|Z = 0, U )}
as re-
quired.
16.4 An alternative fourth condition: monotonicity
Consider again the double-blind randomized trial with randomization indicator
Z, treatment A, and outcome Y . For each individual in the trial, the coun-
terfactual variable A
z=1
is the value of treatment—1 or 0—that an individual
would have taken if he had been assigned to receive treatment (z = 1). The
counterfactual variable A
z=0
is analogously defined as the treatment value if
the individual had been assigned to receive no treatment (z = 0).
If we knew the values of the two counterfactual treatment variables A
z=1
and A
z=0
for each individual, we could classify all individuals in the study
population into four disjoint subpopulations:
1. Always-takers: Individuals who will always take treatment, regardless of
the treatment group they were assigned to. That is, individuals with
both A
z=1
= 1 and A
z=0
= 1.
Figure 16.4
2. Never-takers: Individuals who will never take treatment, regardless of
the treatment group they were assigned to. That is, individuals with
both A
z=1
= 0 and A
z=0
= 0.
3. Compliers or cooperative: Individuals who will take treatment when
assigned to treatment, and no treatment when assigned to no treatment.
That is, individuals with A
z=1
= 1 and A
z=0
= 0.
4. Defiers or contrarians: Individuals who will take no treatment when
assigned to treatment, and treatment when assigned to no treatment.
That is, individuals with A
z=1
= 0 and A
z=0
= 1.
Figure 16.5
Note that these subpopulations—often referred as compliance types or prin-
cipal strata—are not generally identified. If we observe that an individual was
assigned to Z = 1 and took treatment A = 1, we do not know whether she is
a complier or an always-taker. If we observe that an individual was assigned
to Z = 1 and took treatment A = 0, we do not know whether he is a defier or
a never-taker.
When no defiers exist, we say that there is monotonicity because the in-
strument Z either does not change treatment A—as shown in Figure 16.4 for
always-takers and Figure 16.5 for never-takers—or increases the value of treat-
ment A—as shown in Figure 16.6 for compliers. For defiers, the instrument
212 Instrumental variable estimation
Technical Point 16.6
More general structural mean models. Consider an additive structural mean model that allows for continuous and/or
multivariate treatments A, instruments Z, and pre-instrument covariates V . Such model assumes
E
Y − Y
a=0
|Z, A, V
= γ (Z, A, V ; β)
where γ (Z, A, V ; β) is a known function, β is an unknown (possibly vector-valued) parameter, and γ (Z, A = 0, V ; β) =
0. That is, an additive structural mean model is a model for the average causal effect of treatment level A compared
with treatment level 0 among the subset of individuals at level Z of the instrument and level V of the confounders
whose observed treatment is precisely A. The parameters of this model can be identified via g-estimation under the
conditional counterfactual mean independence assumption E
Y
a=0
|Z = 1, V
= E
Y
a=0
|Z = 0, V
.
Analogously, a general multiplicative structural mean model assumes
E [Y |Z, A, V ] = E
Y
a=0
|Z, A, V
exp [γ (Z, A, V ; β)]
where γ (Z, A, V ; β) is a known function, β is an unknown parameter vector, and γ (Z, A = 0, V ; β) = 0. The parameters
of this model can also be identified via g-estimation under analogous conditions. Identification conditions and efficient
estimators for structural mean models were discussed by Robins (1994) and reviewed by Vansteelandt and Goetghebeur
(2003). More generally, g-estimation of nested additive and multiplicative structural mean models can extend IV methods
for time-fixed treatments and confounders to settings with time-varying treatments and confounders.
Z would decrease the value of treatment A—as shown in Figure 16.7. More
generally, monotonicity holds when A
z=1
≥ A
z=0
for all individuals.
Now let us replace any of the homogeneity conditions from the last section
by the monotonicity condition, which will become our new condition (iv). Then
the usual IV estimand does not equal the average causal effect of treatment
E
Y
a=1
−E
Y
a=0
any more. Rather, under monotonicity (iv), the usual IV
estimand equals the average causal effect of treatment in the compliers, that
is
E
Y
a=1
− Y
a=0
|A
z=1
= 1, A
z=0
= 0
.
Technical Point 16.6 shows a proof for this equality under the assumption
Figure 16.6
Figure 16.7
that Z was effectively randomly assigned. As a sketch of the proof, the equality
between the usual IV estimand and the effect in the compliers holds because the
effect of assignment Z on Y —the numerator of the IV estimand—is a weighted
average of the effect of Z in each of the four principal strata. However, the effect
of Z on Y is exactly zero in always-takers and never-takers because the effect
of Z is entirely mediated through A and the value of A in those subpopulations
is fixed, regardless of the value of Z they are assigned to. Also, no defiers exist
under monotonicity (iv). Therefore the numerator of the IV estimand is the
effect of Z on Y in the compliers—which is the same as the effect of A on Y
in the compliers—times the proportion of compliers in the population, which
is precisely the denominator of the usual IV estimand.
In observational studies, the usual IV estimand can also be used to estimate
the effect in the compliers in the absence of defiers. Technically, there are no
compliers or defiers in observational studies because the proposed instrument Z
is not treatment assignment, but the term compliers refers to individuals with
(A
z=1
= 1, A
z=0
= 0) and the term defiers to those with (A
z=1
= 0, A
z=0
= 1).
In our smoking cessation example, the compliers are the individuals who would
quit smoking in a state with high cigarette price and who would not quit
smoking in a state with low price. Conversely, the defiers are the individuals
16.4 An alternative fourth condition: monotonicity 213
who would not quit smoking in a state with high cigarette price and who
would quit smoking in a state with low price. If no defiers exist and the causalThe “compliers average causal ef-
fect” (CACE) is a local average
treatment effect (LATE) in a sub-
population, not the global average
causal effect in the entire popula-
tion. Greenland (2000) refers to
compliers as cooperative, and to
defiers as non-cooperative, to pre-
vent confusion with the concept of
(observed) compliance in random-
ized trials.
instrument is dichotomous (see below and Technical Point 16.6), then 2.4 kg
is the IV effect estimate in the compliers.
The replacement of homogeneity by monotonicity was welcomed in the
mid-1990s as the salvation of IV methods. While homogeneity is often an
implausible condition (iv), monotonicity appeared credible in many settings.
IV methods under monotonicity (iv) cannot identify the average causal effect in
the population, only in the subpopulation of compliers, but that seemed a price
worth paying in order to keep powerful IV methods in our toolbox. However,
the estimation of the average causal effect of treatment in the compliers under
monotonicity (iv) has been criticized on several grounds.
First, the relevance of the effect in the compliers is questionable. The
subpopulation of compliers is not identified and, even though the proportion ofDeaton (2010) on the CACE: “This
goes beyond the old story of look-
ing for an object where the light
is strong enough to see; rather,
we have control over the light, but
choose to let it fall where it may
and then proclaim that whatever it
illuminates is what we were looking
for all along.”
compliers in the population can be calculated (it is the denominator of the usual
IV estimand, see Technical Point 16.7), it varies from instrument to instrument
and from study to study. Therefore, causal inferences about the effect in the
compliers are difficult to use by decision makers. Should they prioritize the
administration of treatment A = 1 to the entire population because treatment
has been estimated to be beneficial among the compliers, which happen to be
6% of the population in our example but could be a smaller or larger group
in the real world? What if treatment is not as beneficial in always-takers
and never-takers, the majority of the population? Unfortunately, the decision
maker cannot know who is included in the 6%. Rather than arguing that the
effect of the compliers is of primary interest, it may be better to accept that
interest in this estimand is not the result of its practical relevance, but ratherA mitigating factor is that, un-
der strong assumptions, investiga-
tors can characterize the compliers
in terms of their distribution of the
observed variables (Angrist and Pis-
chke 2009, Baiocchi et al 2014).
of the (often erroneous) perception that it is easy to identify.
Second, monotonicity is not always a reasonable assumption in observa-
tional studies. The absence of defiers seems a safe assumption in randomized
trials: we do not expect that some individuals will provide consent for partici-
pation in a trial with the perverse intention to do exactly the opposite of what
they are asked to do. Further, monotonicity is ensured by design in trials in
which those assigned to no treatment are prevented from receiving treatment,
i.e., there are no always-takers or defiers. In that scenario, the effect in the
compliers is actually the effect in the treated.
However, monotonicity is harder to justify for some instruments proposed
in observational studies. Consider the proposed instrument “physician pref-
erence” to estimate the treatment effect in patients attending a clinic where
two physicians with different preferences work. The first physician usually
prefers to prescribe the treatment, but she makes exceptions for her patients
with diabetes (because of some known contraindications). The second usuallyThe example to the right was pro-
posed by Swanson and Hern´an
(2014). Also Swanson et al (2015b)
showed empirically the existence of
defiers in an observational setting.
prefers to not prescribe the treatment, but he makes exceptions for his more
physically active patients (because of some perceived benefits). Any patient
who was both physically active and diabetic would have been treated contrary
to both of these physicians’ preferences, and therefore would be labeled as a
defier. That is, monotonicity is unlikely to hold when the decision to treat is
the result of weighing multiple criteria or dimensions of encouragement that
include both risks and benefits. In these settings, the proportion of defiers may
not be negligible.
The situation is even more complicated for the surrogate instruments Z
represented by Figures 16.2 and 16.3. If the causal instrument U
Z
is contin-
uous (e.g., the true, unmeasured physician’s preference), then the standard
IV estimand using a dichotomous surrogate instrument Z (e.g., some mea-
214 Instrumental variable estimation
sured surrogate of preference) is not the effect in a particular subpopulation of
compliers. Rather, the standard IV estimand identifies a particular weighted
average of the effect in all individuals in the population, which makes it diffi-
cult to interpret. Therefore the interpretation of the IV estimand as the effect
in the compliers is questionable when the proposed dichotomous instrument is
not causal, even if monotonicity held for the continuous causal instrument U
Z
Definition of monotonicity for a
continuous causal instrument U
Z
:
A
u
z
is a non-decreasing function
of u
z
on the support of U
Z
(An-
grist and Imbens 1995, Heckman
and Vytlacil 1999).
(see Technical Point 16.7 for details).
Last, but definitely not least important, the partitioning of the popula-
tion into four subpopulations or principal strata may not be justifiable. In
many realistic settings, the subpopulation of compliers is an ill-defined sub-
set of the population. For example, using the proposed instrument “physician
preference” in settings with multiple physicians, all physicians with the same
preference level who could have seen a patient would have to treat the patient
in the exact same way. This is not only an unrealistic assumption, but alsoSwanson et al (2015b) discuss the
difficulties to define monotonicity,
and introduce the concept of global
and local monotonicity in observa-
tional studies.
essentially impossible to define in many observational studies in which it is un-
known which physicians could have seen a patient. A stable partitioning into
compliers, defiers, always takers and never takers also requires deterministic
counterfactuals (not generally required to estimate average causal effects), no
interference (e.g., I may be an always-taker, but decide not to take treatment
when my friend doesn’t), absence of multiple versions of treatment and other
forms of heterogeneity (a complier in one setting, or for a particular instrument,Sommer and Zeger (1991), Imbens
and Rubin (1997), and Greenland
(2000) describe examples of full
compliance in the control group.
may not be a complier in another setting).
In summary, if the effect in the compliers is considered to be of interest,
relying on monotonicity (iv) seems a promising approach in double-blind ran-
domized trials with two arms and all-or-nothing compliance, especially when
one of the arms will exhibit full adherence by design. However, caution is
needed when using this approach in more complex settings and observational
studies, even if the proposed instrument were really an instrument.
16.5 The three instrumental conditions revisited
The previous sections have discussed the relative advantages and disadvantages
of choosing monotonicity or homogeneity as the condition (iv). Our discussion
implicitly assumed that the proposed instrument Z was in fact an instrument.
However, in observational studies, the proposed instrument Z will fail to be a
valid instrument if it violates either of the instrumental conditions (ii) or (iii),
and will be a weak instrument if it only barely meets condition (i).
In all these cases, the use of IV estimation may result in substantial bias
even if condition (iv) held perfectly. We now discuss each of the three instru-
mental conditions.
Condition (i), a Z-A association, is empirically verifiable. Before declaring
Z as their proposed instrument, investigators will check that Z is associated
with treatment A. However, when the Z-A association is weak as in ourIn the context of linear models,
Martens et al. (2006) showed that
instruments are guaranteed to be
weak in the presence of strong con-
founding, because a strong A-U as-
sociation leaves little residual vari-
ation for a strong A-U
Z
, or A-Z,
association.
smoking cessation example, the instrument is said to be weak (see Fine Point
16.2). Three serious problems arise when the proposed instrument is weak.
First, weak instruments yield effect estimates with wide 95% confidence
intervals, as in our smoking cessation example in Section 16.2. Second, weak
instruments amplify bias due to violations of conditions (ii) and (iii). A pro-
posed instrument Z which is weakly associated with treatment A yields a
small denominator of the IV estimator. Therefore, violations of conditions (ii)
and (iii) that affect the numerator of the IV estimator (e.g., unmeasured con-
16.5 The three instrumental conditions revisited 215
Fine Point 16.2
Defining weak instruments There are two related, but different, definitions of weak instrument in the literature:
1. An instrument is (substantively) weak if the true value of the Z-A association—the denominator of the IV
estimand—is “small.”
2. An instrument is (statistically) weak if the F-statistic associated to the observed Z-A association is “small,”
typically meaning less than 10.
In our smoking cessation example, the proposed instrument met both definitions: the risk difference was only 6% and
the F-statistic was a meager 0.8.
The first definition, based on the true value of the Z-A association, reminds us that, even if we had an infinite
sample, the IV estimator greatly amplifies any biases in the numerator when using a proposed weak instrument (the
second problem of weak instruments in the main text). The second definition, based on the statistical properties of
the Z-A association, reminds us that, even if we had a perfect instrument Z, the IV estimator can be biased in finite
samples (the third problem of weak instruments in the main text).
founding for the instrument, a direct effect of the instrument) will be greatly
exaggerated. In our example, any bias affecting the numerator of the IV es-
timator would be multiplied by approximately 15.9 (1/0.0627). Third, evenBound, Jaeger and Baker (1995)
documented this bias. Their pa-
per was followed by many others
that investigated the shortcomings
of weak instruments.
with a valid instrument and a large sample size, weak instruments introduce
bias in the standard IV estimator.
To understand the nature of this third problem, consider a randomly gen-
erated dichotomous variable Z. In an infinite population, the denominator
of the IV estimand will be exactly zero—there is a zero association between
treatment A and a completely random variable—and the IV estimate will be
undefined. However, in a study with a finite sample, chance will lead to an as-
sociation between the randomly generated Z and the unmeasured confounders
U—and therefore between Z and treatment A—that is weak but not exactly
zero. If we propose this random Z as an instrument, the denominator of the
IV estimator will be very small rather than zero. As a result the numerator
will be incorrectly inflated, which will yield potentially very large bias. In fact,Code: Program 16.4
our proposed instrument “Price higher than $1.50” behaves like a randomly
generated variable. Had we decided to define Z as price higher than $1.60,
$1.70, $1.80, or $1.90, the IV estimate would have been 41.3, −40.9, −21.1,
or −12.8 kg, respectively. In each case, the 95% confidence interval around
the estimate was huge. Given how much bias and variability weak instruments
may create, a strong proposed instrument that slightly violates conditions (ii)
and (iii) may be preferable to a less invalid, but weaker, proposed instrument.
Condition (ii), the absence of a direct effect of the instrument on the out-
come, cannot be verified from the data. A deviation from condition (ii) can
be represented by a direct arrow from the instrument Z to the outcome Y , as
shown in Figure 16.8. This direct effect of the instrument that is not mediated
Figure 16.8 through treatment A will contribute to the numerator of the IV estimator, and
it will be incorrectly inflated by the denominator as if it were part of the effect
of treatment A.
Condition (ii) may be violated when a continuous or multi-valued treatment
A is replaced in the analysis by a coarser (e.g., dichotomized) version A
∗
.
Figure 16.9 shows that, even if condition (ii) holds for the original treatment
A, it does not have to hold for its dichotomized version A
∗
, because the path
216 Instrumental variable estimation
Z → A → Y represents a direct effect of the instrument Z that is not mediated
through the treatment A
∗
whose effect is being estimated in the IV analysis.
Figure 16.9
In practice, many treatments are replaced by coarser versions for simplicity of
interpretation. Coarsening of treatment is problematic for IV estimation, but
not necessarily for the methods discussed in previous chapters.
Condition (iii), no confounding for the effect of the instrument on the out-
come, is also unverifiable. Figure 16.10 shows confounding due to common
Figure 16.10
causes of the proposed instrument Z and outcome Y , which may (U
1
) or may
not (U
2
) be causes of treatment A. In observational studies, the possibility of
confounding for the proposed instrument always exists (same as for any other
variable not under the investigator’s control). Confounding contributes to the
numerator of the IV estimator and is incorrectly inflated by the denominator
as if it were part of the effect of treatment A on the outcome Y .
Sometimes condition (iii), and the other conditions too, can appear more
plausible within levels of the measured covariates. Rather than making the
unverifiable assumption that there is absolutely no confounding for the effect
of Z on Y , we might feel more comfortable making the unverifiable assumption
that there is no unmeasured confounding for the effect of Z on Y within levels of
the measured pre-instrument covariates V . We could then apply IV estimation
repeatedly in each stratum of V , and pool the IV effect estimates under the
assumption that the effect in the population (under homogeneity) or in the
compliers (under monotonicity) is constant within levels of V . Alternatively
we could include the variables V as covariates in the two-stage modeling. In
our example, this reduced the size of the effect estimate and increased its 95%
Code: Program 16.5
confidence interval.
Another frequent strategy to support condition (iii) is to check for bal-
anced distributions of the measured confounders across levels of the proposed
instrument Z. The idea is that, if the measured confounders are balanced, it
may be more likely that the unmeasured ones are balanced too. However, this
practice may offer a false sense of security: even small imbalances can lead
to counterintuitively large biases because of the bias amplification discussed
above.
A violation of condition (iii) may occur even in the absence of confound-
ing for the effect of Z on Y . The formal version of condition (iii) requires
exchangeability between individuals with different levels of the proposed in-
strument. Such exchangeability may be violated because of either confounding
(see above) or selection bias. A surprisingly common way in which selection
bias may be introduced in IV analyses is the exclusion of individuals with cer-
tain values of treatment A. For example, if individuals in the population may
receive treatment levels A = 0, A = 1, or A = 2, an IV analysis restricted to
individuals with A = 1 or A = 2 may yield a non-null effect estimate even ifSwanson et al. (2015c) describe
this selection bias in detail. the true causal effect is null. This exclusion does not introduce bias in non-IV
analyses whose goal is to estimate the effect of treatment A = 1 versus A = 2.
All the above problems related to conditions (i)-(iii) are exacerbated in IV
analyses that use simultaneously multiple proposed instruments in an attempt
to alleviate the weakness of a single proposed instrument. Unfortunately, the
larger the number of proposed instruments, the more likely that some of them
will violate one of the instrumental conditions.
16.6 Instrumental variable estimation versus other methods 217
16.6 Instrumental variable estimation versus other methods
IV estimation differs from all previously discussed methods in at least three
aspects.
First, IV estimation replaces the assumption of conditional exchangeabil-
ity by other assumptions. IP weighting and standardization require that the
treated and the untreated are exchangeable conditional on the measured vari-
ables. In contrast, IV estimation can provide valid effect estimates, even if con-
ditional exchangeability does not hold, when conditions (i)-(iv) hold. There-IV estimation is not the only
method that ignores conditional ex-
changeability for identification of
causal effects. Other approaches
like regression discontinuity anal-
ysis (see Fine Point 16.3) and
difference-in-differences (see Tech-
nical Point 7.3) do too.
fore, the choice of method will depend on whether, in a particular research
setting, it is easier to identify and measure the confounders of the effect of A
on Y or to find an instrument Z and expect that there is monotonicity or no
relevant effect heterogeneity.
Second, relatively minor violations of conditions (i)-(iv) for IV estimation
may result in large biases. The foundation of IV estimation is that the denom-
inator blows up the numerator. Therefore, when the conditions do not hold
perfectly or the instrument is weak, there is potential for serious bias in either
direction. As a result, an IV estimate may sometimes be more biased than
an unadjusted estimate. In contrast, IP weighting and standardization tend
to result in slightly biased estimates when their identifiability conditions are
only slightly violated, and adjustment is less likely to introduce a large bias.
The sensitivity of IV estimates to departures from its identifiability conditions
highlights the importance of sensitivity analyses.Baiocchi et al. (2014) review some
approaches to quantify how sensi-
tive IV estimates are to violations
of key assumptions.
Third, the ideal setting for the applicability of standard IV estimation is
more restrictive than that for other methods. As discussed in this chapter,
standard IV estimation is better reserved for settings with lots of unmeasured
confounding, a truly dichotomous and time-fixed treatment A, and a strong
(and causal) proposed instrument Z, and in which either effect homogeneity
or—if one is genuinely interested in the effect in the compliers—monotonicity
is expected to hold. A consequence of these restrictions is that IV estimation
is generally used to answer causal questions about point interventions. For
this reason, IV estimation will not be a prominent method in Part III of this
book, which is devoted to time-varying treatments and the contrast of complex
treatment strategies that are sustained over time.
Causal inference relies on transparency of assumptions and on triangulationTransparency requires proper re-
porting of IV analyses. See some
suggested guidelines by Brookhart
et al (2010), Swanson and Hern´an
(2013), and Baiocchi et al. (2014).
of results from methods that depend on different sets of assumptions. IV
estimation is therefore an attractive approach because it depends on a different
set of assumptions than other methods. However, because of the wide 95%
confidence intervals typical of IV estimates, the value added by using this
approach will often be small. Also, users of IV estimation need to be critically
aware of the limitations of the method. While this statement obviously applies
to any causal inference method, the potentially counterintuitive direction and
magnitude of bias in IV estimation requires especial attention.
218 Instrumental variable estimation
Technical Point 16.7
Monotonicity and the effect in the compliers. Consider a dichotomous causal instrument Z, like the randomization
indicator described in the text, and treatment A. Imbens and Angrist (1994) proved that the usual IV estimand equals
the average causal effect in the compliers E
Y
a=1
− Y
a=0
|A
z=1
− A
z=0
= 1
under monotonicity (iv), i.e., when no
defiers exist. Baker and Lindeman (1994) had a related proof for a binary outcome. See also Angrist, Imbens, and
Rubin (1996), and the associated discussion, and Baker, Kramer, and Lindeman (2016). A proof follows.
The effect of treatment assignment (the intention-to-treat effect) can be written as the weighted average of the
intention-to-treat effects in the four principal strata:
E
Y
z=1
− Y
z=0
= E
Y
z=1
− Y
z=0
|A
z=1
= 1, A
z=0
= 1
Pr
A
z=1
= 1, A
z=0
= 1
(always-takers)
+ E
Y
z=1
− Y
z=0
|A
z=1
= 0, A
z=0
= 0
Pr
A
z=1
= 0, A
z=0
= 0
(never-takers)
+ E
Y
z=1
− Y
z=0
|A
z=1
= 1, A
z=0
= 0
Pr
A
z=1
= 1, A
z=0
= 0
(compliers)
+ E
Y
z=1
− Y
z=0
|A
z=1
= 0, A
z=0
= 1
Pr
A
z=1
= 0, A
z=0
= 1
(defiers)
However, the intention-to-treat effect in both the always-takers and the never-takers is zero, because Z does not
affect A in these two strata and, by individual-level condition (ii) of Technical Point 16.1, Z has no independent effect
on Y . If we assume that no defiers exist, then the above sum is simplified to
E
Y
z=1
− Y
z=0
= E
Y
z=1
− Y
z=0
|A
z=1
= 1, A
z=0
= 0
Pr
A
z=1
= 1, A
z=0
= 0
(compliers).
But, in the compliers, the effect of Z on Y equals the effect of A on Y (because Z = A), that is
E
Y
z=1
− Y
z=0
|A
z=1
= 1, A
z=0
= 0
= E
Y
a=1
− Y
a=0
|A
z=1
= 1, A
z=0
= 0
. Therefore, the effect in the com-
pliers is
E
Y
a=1
− Y
a=0
|A
z=1
= 1, A
z=0
= 0
=
E
Y
z=1
− Y
z=0
Pr [A
z=1
= 1, A
z=0
= 0]
which is the usual IV estimand if we assume that Z is randomly assigned, as random assignment implies
Z⊥⊥{Y
a,z
, A
z
; z = 0, 1; a = 0, 1}. Under this joint independence and consistency, the intention-to-treat ef-
fect E
Y
z=1
− Y
z=0
in the numerator equals E [Y |Z = 1] − E [Y |Z = 0], and the proportion of compliers
Pr
A
z=1
= 1, A
z=0
= 0
in the denominator equals Pr [A = 1|Z = 1] − Pr [A = 1|Z = 0]. To see why the latter
equality holds, note that the proportion of always-takers Pr
A
z=0
= 1
= Pr [A = 1|Z = 0] and the proportion of
never-takers Pr
A
z=1
= 0
= Pr [A = 0|Z = 1]. Since, under monotonicity (iv), there are no defiers, the proportion of
compliers Pr
A
z=1
− A
z=0
= 1
is the remainder 1 − Pr [A = 1|Z = 0] − Pr [A = 0|Z = 1] =
1 − Pr [A = 1|Z = 0] − (1 − Pr [A = 1|Z = 1]) = Pr [A = 1|Z = 1] − Pr [A = 1|Z = 0], which completes the proof.
The above proof only considers the setting depicted in Figure 16.1 in which the instrument Z is causal. When,
as depicted in Figures 16.2 and 16.3, data on a surrogate instrument Z—but not on the causal instrument U
Z
—are
available, Hern´an and Robins (2006b) proved that the average causal effect in the compliers (defined according to U
Z
)
is also identified by the usual IV estimator. Their proof depends critically on two assumptions: that Z is independent
of A and Y given the causal instrument U
Z
, and that U
Z
is binary. However, this independence assumption has often
little substantive plausibility unless U
Z
is continuous. A corollary is that the interpretation of the IV estimand as the
effect in the compliers is questionable in many applications of IV methods to observational data in which Z is at best
a surrogate for U
Z
.
16.6 Instrumental variable estimation versus other methods 219
Fine Point 16.3
Regression discontinuity design. Suppose we are interested in the effect of a new antiviral treatment A on oxygen
levels Y , a continuous outcome measured 1 week later. The treatment is indicated for anyone who arrives at the
hospital with a diagnosis of COVID-19. However, because the treatment is in short supply, the health authorities
prohibit administering the treatment to people under age 65 to guarantee that everybody aged 65 years and older
receives it. That is, the probability of receiving treatment Pr [A = 1|L < 65] = 0 and Pr [A = 1|L ≥ 65] = 1 where L
is age. There is no positivity: the treated and the untreated do not have overlapping values of the confounder L.
In the absence of positivity, we need to make alternative assumptions to identify the causal effect. A reasonable
assumption is that the conditional means of the counterfactual outcomes given L, E
Y
a=1
|L
and E
Y
a=0
|L
, are
continuous in L. In other words, if we could plot these means along the age axis (we can’t because the means are
counterfactual are thus unobserved), we would not observe any jumps in the lines. Under this continuity assumption,
together with the exchangeability assumption that individuals close to both sides of the threshold are comparable, a
discontinuity in the conditional mean of the observed mean given L, E [Y |L], around L = 65 could be interpreted as
a consequence of the probability of treatment changing abruptly at age 65. Whether the mean of Y jumps at the
threshold can be empirically checked by plotting the observed data. (Strictly speaking, we only need continuity around
the threshold L = 65 for our purposes.)
Therefore, under the continuity assumption, we could estimate an average causal effect of A as the difference between
the mean outcome Y in individuals immediately above the threshold (say, those aged 65 years and 1 month) and the
mean outcome in individuals immediately below the threshold (say, those aged 64 years and 11 months). If a bandwidth
of 1 month around the threshold is too small (because too few individuals in the data are in that range), we would
need to increase the bandwidth around the threshold. For example, we could use a bandwidth of 1 year by comparing
individuals aged 64 versus individuals aged 65. The choice of the bandwidth is critical: wide intervals of age may
introduce bias by comparing individuals who are not exchangeable. Once the bandwidth is fixed, we fit linear regression
models on both sides of the threshold L = 65 to estimate the mean outcome on each side of the threshold. To help
determine the bandwidth around the threshold, one can use data-adaptive procedures such as cross-validation (see Fine
Point 18.2). Also, the regression model can include covariates if that is considered necessary to achieve conditional
exchangeability.
The method described above is known as a regression discontinuity design, which was first proposed by Thistlewaite
and Campbell (1960). It can be used when a single covariate L is used to assign treatment, under the continuity
assumption that the relation between L and Y is smooth (i.e., no jumps). A regression discontinuity design estimates
the average causal effect of treatment A on outcome Y in the subset of the population with values of L close to the
threshold. This conditional effect may differ from the average causal effect in the population if L is an effect modifier.
Note that a regression discontinuity design will result in biased estimates of the conditional effect if treatments other
than A also change around the threshold (e.g., if health authorities also restrict the use of scarce intensive care units to
people aged 65 and older) or if high-risk individuals aware of the threshold manipulate their own data (e.g., if at risk
individuals aged 63 and 64 find a way to provide fake documentation that shows an older age).
More specifically, we have described here a sharp regression discontinuity design in which the probability of treatments
jumps from 0 to 1 at the threshold. A fuzzy regression discontinuity design is an extension of the method that allows
the jump in the probability of treatment from a value greater than 0 to a value less than 1. This extension, which
relies on the monotonicity assumption, estimates the average causal effect in a subset of a subset of the population: the
compliers with values of L close to the threshold. For estimation details see Hahn, Todd and van der Klaauw (2001)
and Imbens and Lemieux (2008).
220 Instrumental variable estimation
Chapter 17
CAUSAL SURVIVAL ANALYSIS
In previous chapters we have been concerned with causal questions about the treatment effects on outcomes
occurring at a particular time point. For example, we have estimated the effect of smoking cessation on weight
gain measured in the year 1982. Many causal questions, however, are concerned with treatment effects on the time
until the occurrence of an event of interest. For example, we may want to estimate the causal effect of smoking
cessation on the time until death, whenever death occurs. This is an example of a survival analysis.
The use of the word “survival” does not imply that the event of interest must be death. The term “survival
analysis”, or the equivalent term “failure time analysis”, is applied to any analyses about time to an event, where
the event may be death, marriage, incarceration, cancer, flu infection, etc. Survival analyses require some special
considerations and techniques because the failure time of many individuals may occur after the study has ended
and is therefore unknown. This chapter outlines basic techniques for survival analysis in the simplified setting of
time-fixed treatments.
17.1 Hazards and risks
Suppose we want to estimate the average causal effect of smoking cessation
A (1: yes, 0: no) on the time to death T with time measured from the start
of follow-up. This is an example of a survival analysis: the outcome is time
to an event of interest that can occur at any time after the start of follow-
up. In most follow-up studies, the event of interest is not observed to happen
for all, or even the majority of, individuals in the study. This is so because
most follow-up studies have a date after which there is no information on any
individuals: the administrative end of follow-up.
After the administrative end of follow-up, no additional data can be used.
Individuals who do not develop the event of interest before the administrative
end of follow-up have their survival time administratively censored, i.e., we
know that they survived beyond the administrative end of follow-up, but we
do not know for how much longer. For example, let us say that we conduct
the above survival analysis among the 1629 cigarette smokers from the NHEFS
who were aged 25-74 years at baseline and who were alive through 1982. For
all individuals, the start of follow-up is January 1, 1983 and the administrative
end of follow-up is December 31, 1992. We define the administrative censoring
time to be the difference between the date of administrative end of follow-up
and date at which follow-up begins. In our example, this time is the same—120
months—for all individuals because the start of follow-up and the administra-In a study with staggered entry
(i.e., with a variable start of follow-
up date) different individuals will
have different administrative cen-
soring times, even when the admin-
istrative end of follow-up date is
common to all.
tive end of follow-up are the same for everybody. Of the 1629 individuals,
only 318 individuals died before the end of 1992, so the survival time of the
remaining 1311 individuals is administratively censored.
Administrative censoring is a problem intrinsic to survival analyses—studies
of smoking cessation and death will rarely, if ever, follow a cohort of individuals
until extinction—but administrative censoring is not the only type of censoring
that may occur in survival analyses. Like any other causal analyses, survival
222 Causal survival analysis
Fine Point 17.1
Competing events As described in Section 8.5, a competing event is an event (typically, death) that prevents the event
of interest (e.g., stroke) from happening: individual who die from other causes (say, cancer) cannot ever develop stroke.
In survival analyses, the key decision is whether to consider competing events a form of non-administrative censoring.
• If the competing event is considered a censoring event, then the analysis is effectively an attempt to simulate
a population in which death from other causes is somehow either abolished or rendered independent of the risk
factors for stroke. The resulting effect estimate is hard to interpret and may not correspond to a meaningful
estimand (see Chapter 8). In addition, the censoring may introduce selection bias under the null, which would
require adjustment (by, say, IP weighting) using data on the measured risk factors for the event of interest.
• If the competing event is not considered a censoring event, then the analysis effectively sets the time to event
to be infinite. That is, dead individuals are considered to have probability zero of developing stroke between
their death and the administrative end of follow-up. The estimate of the effect of treatment on stroke is hard to
interpret because a non-null estimate may arise from a direct effect of treatment on death, which would prevent
the occurrence of stroke.
An alternative to the handling of competing events is to create a composite event that includes both the competing
event and the event of interest (e.g., death and stroke) and conduct a survival analysis for the composite event.
This approach effectively eliminates the competing events, but fundamentally changes the causal question. Again, the
resulting effect estimate is hard to interpret because a non-null estimate may arise from either an effect of treatment
on stroke or on death. Another alternative is to restrict the inference to the principal stratum of individuals who would
not die regardless of the treatment level they received. This approach targets a sort of local average effect, as defined
in Chapter 16, which makes both interpretation and valid estimation especially challenging.
None of the above strategies provides a satisfactory solution to the problem of competing events. Indeed the presence
of competing events raises logical questions about the meaning of the causal estimand that cannot be bypassed by
statistical techniques. For a detailed description of approaches to handle competing events and their challenges, see
the discussion by Young et al. (2019). More recently, Stensrud et al. (2020, 2021) proposed an approach based on
separable effects, a concept discussed in Technical Point 23.3.
analysis may also need to handle non-administrative types of censoring, such
as loss to follow-up (e.g., dropout from the study) and competing events (see
Fine Point 17.1). In previous chapters we have discussed how to adjust for the
selection bias introduced by non-administrative censoring via standardization
or IP weighting. The same approaches can be applied to survival analyses.
Therefore, in this chapter, we will focus on administrative censoring. We defer
a more detailed consideration of non-administrative censoring to Part III of the
book because non-administrative censoring is generally a time-varying process,
whereas the time of administrative censoring is fixed at baseline.For simplicity, we assume that any-
one without confirmed death sur-
vived the follow-up period. In real-
ity, some individuals may have died
but confirmation (by, say, a death
certificate or a proxy interview) was
not feasible. Also for simplicity, we
will ignore the problem described in
Fine Point 12.1.
In our example, the month of death T can take values subsequent from 1
(January 1983) to 120 (December 1992). T is known for 102 treated (A = 1)
and 216 untreated (A = 0) individuals who died during the follow-up, and is
administratively censored (that is, all we know is that it is greater than 120
months) for the remaining 1311 individuals. Therefore we cannot compute the
mean survival
b
E[T ] as we did in previous chapters with the outcome of interest.
Rather, in survival analysis we need to use other measures that can accom-
modate administrative censoring. Some common measures are the survival
probability, the risk, and the hazard. Let us define these quantities, which are
functions of the survival time T .
The survival probability Pr [T > k], or simply the survival at month k, is
17.2 From hazards to risks 223
the proportion of individuals who survived through time k. If we calculate the
survivals at each month until the administrative end of follow-up k
end
= 120
and plot them along a horizontal time axis, we obtain the survival curve.
The survival curve starts at Pr [T > 0] = 1 for k = 0 and then decreases
monotonically—that is, it does not increase—with subsequent values of k =
1, 2, ...k
end
. Alternatively, we can define risk, or cumulative incidence, at time
k as one minus the survival 1 − Pr [T > k] = Pr [T ≤ k]. The cumulative
incidence curve starts at Pr [T ≤ 0] = 0 and increases monotonically during
the follow-up.
In survival analyses, a natural approach to quantify the treatment effect isOther effect measures that can be
derived from survival curves are
years of life lost and the restricted
mean survival time.
to compare the survival or risk under each treatment level at some or all times
k. Of course, in our smoking cessation example, a contrast of these curves
may not have a causal interpretation because the treated and the untreated
are probably not exchangeable. However, suppose for a second (actually, until
Figure 17.1
Section 17.4) that quitters (A = 1) and non-quitters (A = 0) are marginally
exchangeable. Then we can construct the survival curves shown in Figure 17.1
and compare Pr [T > k|A = 1] versus Pr [T > k|A = 0] for all times k. For
example, the survival at 120 months was 76.2% among quitters and 82.0%
among non-quitters. Alternatively, we could contrast the risks rather than the
survivals. For example, the 120-month risk was 23.8% among quitters and
18.0% among non-quitters.
Code: Program 17.1
A conventional statistical test to
compare survival curves (the log-
rank test) yielded a P-value=
0.005.
At any time k, we can also calculate the proportion of individuals who
develop the event among those who had not developed it before k. This is
the hazard Pr [T = k|T > k − 1]. Technically, this is the discrete time hazard,
i.e., the hazard in a study in which time is measured in discrete intervals—
as opposed to measured continuously. Because in real-world studies, time is
indeed measured in discrete intervals (years, months, weeks, days...) rather
than in a truly continuous fashion, here we will refer to the discrete time
hazard as, simply, the hazard.
The risk and the hazard are different measures. The denominator of the
risk—the number of individuals at baseline—is constant across times k and its
numerator—all events between baseline and k—is cumulative. That is, the risk
will stay flat or increase as k increases. On the other hand, the denominator
of the hazard—the number of individuals alive at k—varies over time t and
its numerator includes only recent events—those during interval k. That is,
the hazard may increase or decrease over time. In our example, the hazard at
120 months was 0% among quitters (because the last death happened at 113
months in this group) and 1/986 = 0.10% among non-quitters, and the hazard
curves between 0 and 120 months had roughly the shape of a letter M.
A frequent approach to quantify the treatment effect in survival analyses
is to estimate the ratio of the hazards in the treated and the untreated, known
as the hazard ratio. However, the hazard ratio is problematic for the reasons
described in Fine Point 17.2. Therefore, the survival analyses in this book
privilege survival/risk over hazard. However, that does not mean that we
should completely ignore hazards. The estimation of hazards is often a useful
intermediate step for the estimation of survivals and risks.
17.2 From hazards to risks
In survival analyses, there are two main ways to arrange the analytic dataset.
In the first data arrangement each row of the database corresponds to one
224 Causal survival analysis
person. This data format—often referred to as the “wide”format when there
are time-varying treatments and confounders—is the one we have used so far
in this book. In the analyses of the previous section, the dataset had 1629
rows, one per individual.
In the second data arrangement each row of the database corresponds to
a person-time. That is, the first row contains the information for person 1
at k = 0, the second row the information for person one at k = 1, the third
row the information for person 1 at k = 2, and so on until the follow-up
of person one ends. The next row contains the information of person 2 at
k = 0, etc. This person-time (or “long”) data format is the one we will use
in most survival analyses in this chapter and in all analyses with time-varying
treatments in Part III. In our smoking cessation example, the person-time
dataset has 176, 764 rows, one per person-month.
To encode survival information through k in the person-time data format,
it is helpful to define a time-varying indicator of event D
k
. For each person
at each month k, the indicator D
k
takes value 1 if T ≤ k and value 0 if
T > k. The causal diagram in Figure 17.2 shows the treatment A and the
Figure 17.2 event indicators D
1
and D
2
at times 1 and 2, respectively. The variable U
represents the (generally unmeasured) factors that increase susceptibility to
the event of interest. Note that sometimes these susceptibility factors are
time-varying too. In that case, they can be depicted in the causal diagram as
U
0
, U
1
..., and so on. Part III deals with the case in which the treatment itself
is time-varying.
In the person-time data format, the row for a particular individual at time
k includes the indicator D
k+1
. In our example, the first row of the person-
time dataset, for individual one at k = 0, includes the indicator D
1
, which isBy definition, everybody had to sur-
vive month 0 in order to be in-
cluded in the dataset, i.e., D
0
= 0
for all individuals.
1 if the individual died during month 1 and 0 otherwise; the second row, for
individual one at k = 1, includes the indicator D
2
, which is 1 if the individual
died during month 2 and 0 otherwise; and so on. The last row in the dataset for
each individual is either her first row with D
k+1
= 1 or the row corresponding
to month 119.
Using the time-varying outcome variable D
k
, we can define survival at k as
Pr [D
k
= 0], which is equal to Pr [T > k], and risk at k as Pr [D
k
= 1], which is
equal to Pr [T ≤ k]. The hazard at k is defined as Pr [D
k
= 1|D
k−1
= 0]. For
k = 1 the hazard is equal to the risk because everybody is, by definition, alive
at k = 0.
The survival probability at k is the product of the conditional probabilities
of having survived each interval between 0 and k. For example, the survival
at k = 2, Pr [D
2
= 0], is equal to survival probability at k = 1, Pr [D
1
= 0],
times the survival probability at k = 2 conditional on having survived through
k = 1, Pr [D
2
= 0|D
1
= 0]. More generally, the survival at k is
Pr [D
k
= 0] =
k
Y
m=1
Pr [D
m
= 0|D
m−1
= 0]
That is, the survival at k equals the product of one minus the hazard at all
previous times. If we know the hazards through k we can easily compute the
survival at k (or the risk at k, which is just one minus the survival).
The hazard at k, Pr [D
k
= 1|D
k−1
= 0], can be estimated nonparametri-
cally by dividing the number of cases during the interval k by the number of
individuals alive at the end of interval k − 1. If we substitute this estimate
into the above formula the resulting nonparametric estimate of the survival
Pr [D
k
= 0] at k is referred to as the Kaplan-Meier, or product-limit, estima-
17.2 From hazards to risks 225
Fine Point 17.2
The hazards of hazard ratios When using the hazard ratio as a measure of causal effect, two important properties of
the hazard ratio need to be taken into account.
First, because the hazards vary over time, the hazard ratio generally does too. That is, the ratio at time k may differ
from that at time k + 1. However, many published survival analyses report a single hazard ratio, which is usually the
consequence of fitting a Cox proportional hazards model that assumes a constant hazard ratio by ignoring interactions
with time. The reported hazard ratio is a weighted average of the k-specific hazard ratios, which makes it hard to
interpret. If the risk is rare and censoring only occurs at a common administrative censoring time k
end
, then the weight
of the hazard ratio at time k is proportional to the total number of events among untreated individuals that occur at
k. (Technically, the weights are equal to the conditional density at k of T given A = 0 and T < k
end
.) Because it is a
weighted average, the reported hazard ratio may be 1 even if the survival curves are not identical. In contrast to “the”
hazard ratio, ratios and differences of survival probabilities and risks are defined with respect to a fixed time period,
e.g., the 5-year survival difference, the 120-month risk ratio.
Second, even if we presented the time-specific hazard ratios, their causal interpretation is not straightforward. Suppose
treatment kills all high-risk individuals by time k and has no effects on others. Then the hazard ratio at time k + 1
compares the treated and the untreated individuals who survived through k. In the treated group, the survivors are
all low-risk individuals (because the high-risk ones have already been killed by treatment); in the untreated group, the
survivors are a mixture of high-risk and low-risk individuals (because treatment did not weed out the former). As a
result the hazard ratio at k + 1 will be less than 1 even though treatment is not beneficial for any individual.
This apparent paradox is an example of selection bias due to conditioning on a post-treatment variable (i.e., being alive
at k) which is affected by treatment. For example, the hazard ratio at time 2 is the probability Pr [D
2
= 1|D
1
= 0, A]
of the event at time 2 among those who survived time 1. As depicted in the causal diagram of Figure 17.3, the
conditioning on the collider D
1
will generally open the path A → D
1
← U → D
2
and therefore induce an association
between treatment A and event D
2
among those with D
1
= 0. This built-in selection bias of hazard ratios does not
happen if the survival curves are the same in the treated and the untreated, i.e., if there are no arrows from A into the
indicators for the event. Hern´an (2010) described an example of this problem.
tor. Figure 17.1 was constructed using the Kaplan-Meier estimator, which is
an excellent estimator of the survival curve, provided the total number of fail-
ures over the follow up period is reasonably large. Typically, the number of
Figure 17.3
cases during each interval is low (or even zero) and thus the nonparametric
estimates of the hazard Pr [D
k
= 1|D
k−1
= 0] at k will be very unstable. If
our interest is in estimation of the hazard at a particular k, smoothing via a
parametric model may be required (see Chapter 11 and Fine Point 17.3).
An easy way to parametrically estimate the hazards is to fit a logistic
regression model for Pr [D
k+1
= 1|D
k
= 0] that, at each k, is restricted to
individuals who survived through k. The fit of this model is straightforward
when using the person-time data format. In our example, we can estimate the
hazards in the treated and the untreated by fitting the logistic model
logit Pr [D
k+1
= 1|D
k
= 0, A] = θ
0,k
+ θ
1
A + θ
2
A × k + θ
3
A × k
2
where θ
0,k
is a time-varying intercept that can be estimated by some flexibleAlthough each person occurs in
multiple rows of the person-time
data structure, the standard er-
ror of the parameter estimates out-
putted by a routine logistic regres-
sion program will be correct if the
hazards model is correct.
function of time such as θ
0,k
= θ
0
+ θ
4
k + θ
5
k
2
. The flexible time-varying
intercept allows for a time-varying hazard and the product terms between
treatment A and time (θ
2
A ×k + θ
3
A ×k
2
) allow the hazard ratio to vary over
time. See Technical Point 17.1 for details on how a logistic model approximates
a hazards model. Functions other than the logit (e.g., the probit) can also be
used to model dichotomous outcomes and therefore to estimate hazards.
We then compute estimates of the survival Pr [D
k+1
= 0|A = a] by multi-
plying the estimates of one minus the estimates of Pr [D
k+1
= 1|D
k
= 0, A = a]
226 Causal survival analysis
Fine Point 17.3
Models for survival analysis. Methods for survival analysis need to accommodate the expected censoring of failure
times due to administrative end of follow-up.
Nonparametric approaches to survival analysis, like constructing Kaplan-Meier curves, make no assumptions about the
distribution of the unobserved failure times due to administrative censoring. On the other hand, parametric models for
survival analysis assume a particular statistical distribution (e.g., exponential, Weibull) for the failure times or hazards.
The logistic model described in the main text to estimate hazards is an example of a parametric model.
Other models for survival analysis, like the Cox proportional hazards model and the accelerated failure time (AFT)
model, do not assume a particular distribution for the failure times or hazards. In particular, these models are agnostic
about the shape of the hazard when all covariates in the model have value zero—often referred to as the baseline hazard.
These models, however, impose a priori restrictions on the relation between the baseline hazard and the hazard under
other combinations of covariate values. As a result, these methods are referred to as semiparametric methods.
See the book by Hosmer, Lemeshow, and May (2008) for a review of applied survival analysis. More formal descriptions
can be found in the books by Fleming and Harrington (2005) and Kalbfleisch and Prentice (2002).
provided by the logistic model, separately for the treated and the untreated.Code: Program 17.2
Figure 17.4 shows the survival curves obtained after parametric estimation of
the hazards. These curves are a smooth version of those in Figure 17.1.
The validity of this procedure requires no misspecification of the hazards
model. In our example, this assumption seems plausible because we obtained
essentially the same survival estimates as in the previous section when we
estimated the survival in a fully nonparametric way. A 95% confidence interval
around the survival estimates can be easily constructed via bootstrapping of
the individuals in the population.
17.3 Why censoring matters
The only source of censoring in our study is a common administrative censoring
time k
end
= 120 that is identical for all individuals. In this simple setting the
Figure 17.4
procedure described in the previous section to estimate the survival is overkill.
One can simply estimate the survival probabilities Pr [D
k+1
= 0|A = a] by the
fraction of individuals who received treatment a and survived to k + 1, or
by fitting separate logistic models for Pr [D
k+1
= 0|A] at each time, for k =
0, 1, ..., k
end
.
Now suppose that individuals start the follow-up at different dates—there
is staggered entry into the study—but the administrative end of follow-up date
is common to all. Because the administrative censoring time is the difference
between the administrative end of follow-up and the time of start of follow-
up, different individuals will have different administrative censoring times. In
this setting it is helpful to define a time-varying indicator C
k
for censoring
by time k. For each person at each month k, the indicator C
k
takes value 0
if the administrative end of follow-up is greater than k and 1 otherwise. In
the person-time data format, the row for a particular individual at time k
includes the indicator C
k+1
. We did not include this variable in our dataset
because C
k+1
= 0 for all individuals at all times k before 120 months. In the
general case with random (i.e., individual-specific) administrative censoring,
the indicator C
k+1
will transition from 0 to 1 at different times k for different
17.3 Why censoring matters 227
Technical Point 17.1
Approximating the hazard ratio via a logistic model. The (discrete-time) hazard ratio
Pr[D
k+1
=1|D
k
=0,A=1]
Pr[D
k+1
=1|D
k
=0,A=0]
is
exp (α
1
) at all times k +1 in the hazards model Pr [D
k+1
= 1|D
k
= 0, A] = Pr [D
k+1
= 1|D
k
= 0, A = 0]×exp (α
1
A).
If we take logs on both sides of the equation, we obtain log Pr [D
k+1
= 1|D
k
= 0, A] = α
0,k
+ α
1
A where α
0,k
=
log Pr [D
k+1
= 1|D
k
= 0, A = 0].
Suppose the hazard at k + 1 is small, i.e., Pr [D
k+1
= 1|D
k
= 0, A] ≈ 0. Then one minus the hazard at k + 1 is
close to one, and the hazard is approximately equal to the odds: Pr [D
k+1
= 1|D
k
= 0, A] ≈
Pr[D
k+1
=1|D
k
=0,A]
Pr[D
k+1
=0|D
k
=0,A]
. We
then have
log
Pr [D
k+1
= 1|D
k
= 0, A]
Pr [D
k+1
= 0|D
k
= 0, A]
= logit Pr [D
k+1
= 1|D
k
= 0, A] ≈ α
0,k
+ α
1
A
That is, if the hazard is close to zero at k + 1, we can approximate the log hazard ratio α
1
by θ
1
in a logistic model
logit Pr [D
k+1
= 1|D
k
= 0, A] = θ
0,k
+ θ
1
A like the one we used in the main text (Thompson 1977). As a rule of
thumb, the approximation is often considered to be accurate enough when Pr [D
k+1
= 1|D
k
= 0, A] < 0.1 for all k.
This rare event condition can almost always be guaranteed to hold: we just need to define a time unit k that is short
enough for Pr [D
k+1
= 1|D
k
= 0, A] < 0.1. For example, if D
k
stands for lung cancer, k may be measured in years; if
D
k
stands for infection with the common cold virus, k may be measured in days. The shorter the time unit, the more
rows in the person-time dataset used to fit the logistic model.
people.
Our goal is to estimate the survival curve that would have been observed if
nobody had been censored before k
end
, where k
end
is the maximum administra-
tive censoring time in the study. That is, our goal is to estimate the survival
Pr [D
k
= 0|A = a] that would have been observed if the value of the time-
varying indicators D
k
were known even after censoring. Technically, we can
also refer to this quantity as Pr
h
D
c=0
k
= 0|A = a
i
where c = (c
1
, c
2
...c
k
end
).
As discussed in Chapter 12, the use of the superscript c = 0 makes explicit the
quantity that we have in mind. We sometimes choose to omit the superscript
c = 0 when no confusion can arise. For simplicity, suppose that the time of
start of follow-up was as if randomly assigned to each individual, which would
be the case if there were no secular trends in any variable. Then the admin-
istrative censoring time, and therefore the indicator C, is independent of both
treatment and death time.
We cannot validly estimate this survival Pr [D
k
= 0|A = a] at time k by
simply computing the fraction of individuals who received treatment level a and
survived and were not censored through k. This fraction is a valid estimator
of the joint probability Pr [C
k+1
= 0, D
k+1
= 0|A = a], which is not what we
want. To see why, consider a study with k
end
= 2 and in which the following
happens:
• Pr [C
1
= 0] = 1, i.e., nobody is censored by k = 1
• Pr [D
1
= 0|C
0
= 0] = 0.9, i.e., 90% of individuals survive through k = 1
• Pr [C
2
= 0|D
1
= 0, C
1
= 0] = 0.5, i.e., a random half of survivors is cen-
sored by k = 2
• Pr [D
2
= 0|C
2
= 0, D
1
= 0, C
1
= 0] = 0.9, i.e., 90% of the remaining in-
dividuals survive through k = 2
The fraction of uncensored survivors at k = 2 is 1 ×0.9 ×0.5 ×0.9 = 0.405.
However, if nobody had been censored, i.e., if Pr [C
2
= 0|D
1
= 0, C
1
= 0] =
228 Causal survival analysis
1, the survival would have been 1 × 0.9 × 1 × 0.9 = 0.81. This example
motivates how correct estimation of the survivals Pr [D
k
= 0|A = a] requires
the procedures described in the previous section. Specifically, under (as if)
randomly assigned censoring, the survival Pr [D
k
= 0|A = a] at k is
k
Y
m=1
Pr [D
m
= 0|D
m−1
= 0, C
m
= 0, A = a] for k < k
end
The estimation procedure is the same as described above except that we either
use a nonparametric estimate of, or fit a logistic model for, the cause-specific
hazard Pr [D
k+1
= 1|D
k
= 0, C
k+1
= 0, A = a].
Often we are not ready to assume that censoring is as if randomly assigned.
When there is staggered entry, an individual’s time of administrative censoring
depends on the calendar time at study entry (later entries have shorter values
of k
end
) and calendar time may itself be associated with the outcome. There-
fore, the above procedure will need to be adjusted for baseline calendar time.
In addition, there may be other baseline prognostic factors that are unequally
distributed between the treated (A = 1) and the untreated (A = 0), which also
requires adjustment. The next sections extend the above procedure to incorpo-
rate adjustment for baseline confounders via g-methods. In Part III we extend
the procedure to settings with time-varying treatments and confounders.
17.4 IP weighting of marginal structural models
When the treated and the untreated are not exchangeable, a direct contrast
of their survival curves cannot be endowed with a causal interpretation. In
our smoking cessation example, we estimated that the 120-month survival was
lower in quitters than in non-quitters (76.2% versus 82.0%), but that does not
necessarily imply that smoking cessation increases mortality. Older people are
more likely to quit smoking and also more likely to die. This confounding by
age makes smoking cessation look bad because the proportion of older people
is greater among quitters than among non-quitters.
Let us define D
a,c=0
k
as a counterfactual time-varying indicator for death
at k under treatment level a and no censoring. For simplicity of notation, we
will write D
a,c=0
k
as D
a
k
when, as in this chapter, it is clear that the goal is
estimating the survival in the absence of censoring. For additional simplicity, in
the remainder of this chapter we omit C
k
= 0 from the conditioning event of the
hazard at k, Pr [D
k+1
= 0|D
k
= 0, L = l, A]. That is, we write all expressions
as if all individuals had a common administrative censoring time, like in our
smoking cessation example.
Suppose we want to compare the counterfactual survivals Pr
D
a=1
k+1
= 0
and Pr
D
a=0
k+1
= 0
that would have been observed if everybody had received
treatment (a = 1) and no treatment (a = 0), respectively. That is, the causal
contrast of interest is
Pr
D
a=1
k+1
= 0
vs. Pr
D
a=0
k+1
= 0
for k = 0, 2, ...k
end
− 1
Because of confounding, this contrast may not be validly estimated by the
contrast of the survivals Pr [D
k+1
= 0|A = 1] and Pr [D
k+1
= 0|A = 0] that we
described in the previous sections. Rather, a valid estimation of the quan-
tities Pr
D
a
k+1
= 0
for a = 1 and a = 0 typically requires adjustment for
17.4 IP weighting of marginal structural models 229
confounders, which can be achieved through several methods. This section
focuses on IP weighting. Let us assume that the treated (A = 1) and the
Figure 17.5
untreated (A = 0) are exchangeable within levels of the L variables, as rep-
resented in the causal diagram of Figure 17.5. Like in Chapters 12 to 15,
L includes the variables sex, age, race, education, intensity and duration of
smoking, physical activity in daily life, recreational exercise, and weight. We
also assume positivity and consistency. The estimation of IP weighted survival
curves has two steps.
First, we estimate the stabilized IP weight SW
A
for each individual in
the study population. The procedure is exactly the same as the one de-
scribed in Chapter 12. We fit a logistic model for the conditional probabil-
ity Pr [A = 1|L] of treatment (i.e., smoking cessation) given the variables in
L. The denominator of the estimated SW
A
is
c
Pr [A = 1|L] for treated indi-Code: Program 17.3
viduals and
1 −
c
Pr [A = 1|L]
for untreated individuals, where
c
Pr [A = 1|L]
is the predicted value from the logistic model. The numerator of the esti-
mated weight SW
A
is
c
Pr [A = 1] for the treated and
1 −
c
Pr [A = 1]
for the
untreated, where
c
Pr [A = 1] can be estimated nonparametrically or as the pre-
dicted value from a logistic model for the marginal probability Pr [A = 1] of
treatment. See Chapter 11 for details on predicted values.
The application of the estimated weights SW
A
creates a pseudo-population
in which the variables in L are independent from the treatment A, which
eliminates confounding by those variables. In our example, the weights had
mean 1 (as expected) and ranged from 0.33 to 4.21.
Second, using the person-time data format, we fit a hazards model like the
one described above except that individuals are weighted by their estimated
SW
A
. Technically, this IP weighted logistic model estimates the parameters
of the marginal structural logistic model
logit Pr
D
a
k+1
= 0|D
a
k
= 0
= β
0,k
+ β
1
a + β
2
a × k + β
3
a × k
2
That is, the IP weighted model estimates the time-varying hazards that would
have been observed if all individuals in the study population had been treated
(a = 1) and the time-varying hazards if they had been untreated (a = 0).
Figure 17.6
The estimates of Pr
D
a
k+1
= 0|D
a
k
= 0
from the IP weighted hazards mod-
els can then be multiplied over time (see previous section) to obtain an estimate
of the survival Pr
D
a
k+1
= 0
that would have been observed under treatment
a = 1 and under no treatment a = 0. The resulting curves are shown in Figure
17.6.
In our example, the 120-month survival estimates were 80.7% under smok-
ing cessation and 80.5% under no smoking cessation; difference 0.2% (95% con-
fidence interval from −4.1% to 3.7% based on 500 bootstrap samples). Though
the survival curve under treatment was lower than the curve under no treat-
ment for most of the follow-up, the maximum difference never exceeded −1.4%
with a 95% confidence interval from −3.4% to 0.7%. That is, after adjustment
for the covariates L via IP weighting, we found little evidence of an effect of
smoking cessation on mortality at any time during the follow-up. The validity
of this procedure requires no misspecification of both the treatment model and
the marginal hazards model.
230 Causal survival analysis
17.5 The parametric g-formula
In the previous section we estimated the survival curve under treatment and
under no treatment in the entire study population via IP weighting. To do
so, we adjusted for L and assumed exchangeability, positivity, and consis-
tency. Another method to estimate the marginal survival curves under those
assumptions is standardization based on parametric models, i.e., the paramet-
ric g-formula.
The survival Pr
D
a
k+1
= 0
at k +1 under treatment level a is the weighted
average of the survival conditional probabilities at k + 1 within levels of the
covariates L and treatment level A = a, with the proportion of individuals in
each level l of L as the weights. That is, under exchangeability, positivity, and
consistency, Pr
D
a
k+1
= 0
equals the standardized survival
X
l
Pr [D
k+1
= 0|L = l, A = a] Pr [L = l] .
For a formal proof, see Section 2.3.
Therefore, the estimation of the parametric g-formula has two steps. First,
we need to estimate the conditional survivals Pr [D
k+1
= 0|L = l, A = a] using
our administratively censored data. Second, we need to compute their weighted
average over all values l of the covariates L. We describe each of these two
steps in our smoking cessation example.
For the first step we fit a parametric hazards model like the one described
in Section 17.2, except that the variables in L are included as covariates. If
the model is correctly specified, it validly estimates the time-varying hazards
Pr [D
k+1
= 1|D
k
= 0, L, A] within levels of treatment A and covariates L. The
Figure 17.7
product of one minus the conditional hazards
k
Y
m=0
Pr [D
m+1
= 0|D
m
= 0, L = l, A = a]
is equal to the conditional survival Pr [D
k+1
= 0|L = l, A = a]. Because of
conditional exchangeability given L, the conditional survival for a particular
set of covariate values L = l and A = a can be causally interpreted as the
survival that would have been observed if everybody with that set of covariates
had received treatment value a. That is,
Pr [D
k+1
= 0|L = l, A = a] = Pr
D
a
k+1
= 0|L = l
Therefore the conditional hazards can be used to estimate the survival curve
under treatment (a = 1) and no treatment (a = 0) within each combination
of values l of L. For example, we can use this model to estimate the survivalIn Chapter 12 we referred to models
conditional on all the covariates L
as faux marginal structural models.
curves under treatment and no treatment for white men aged 61, with college
education, low levels of exercise, etc. However, our goal is estimating the
marginal, not the conditional, survival curves under treatment and under no
treatment.
For the second step we compute the weighted average of the conditional
survival across all values l of the covariates L, i.e., we standardize the survivalCode: Program 17.4
The procedure is analogous to the
one described in Chapter 13.
to the confounder distribution. To do so, we use the method described in Sec-
tion 13.3 to standardize means: standardization by averaging after expansion
of dataset, outcome modeling, and prediction. This method can be used even
when some of the variables in L are continuous so that the sum over values l
is formally an integral. The resulting curves are shown in Figure 17.7.
17.6 G-estimation of structural nested models 231
In our example, the survival curve under treatment was lower than the curve
under no treatment during the entire follow-up, but the maximum difference
never exceeded −2.0% (95% confidence interval from −5.6% to 1.8%). The 120-
month survival estimates were 80.4% under smoking cessation and 80.6% under
no smoking cessation; difference 0.2% (95% confidence interval from −4.6% to
4.1%). That is, after adjustment for the covariates L via standardization, we
found little evidence of an effect of smoking cessation on mortality at any time
during the follow-up. Note that the survival curves estimated via IP weighting
(previous section) and the parametric g-formula (this section) are similar but
not identical because they rely on different parametric assumptions: the IP
weighted estimates require no misspecification of a model for treatment and
a model for the unconditional hazards; the parametric g-formula estimates
require no misspecification of a model for the conditional hazards.
17.6 G-estimation of structural nested models
The previous sections describe causal contrasts that compare survivals, or risks,
under different levels of treatment A. The survival was computed from haz-
ards estimated by logistic regression models. This approach is feasible when
the analytic method is IP weighting of marginal structural models or the para-
metric g-formula, but not when the method is g-estimation of structural nested
models. As explained in Chapter 14, structural nested models are models for
conditional causal contrasts (e.g., the difference or ratio of covariate-specific
means under different treatment levels), not for the components of those con-
trasts (e.g., each of the means under different treatment levels). Therefore weIn fact, we may not even approxi-
mate a hazard ratio because struc-
tural nested logistic models do not
generalize easily to time-varying
treatments (Technical Point 14.1).
cannot estimate survivals or hazards using a structural nested model.
We can, however, consider a structural nested log-linear model to model
the ratio of cumulative incidences (i.e., risks) under different treatment levels.
Structural nested cumulative failure time models do precisely that (see Tech-
nical Point 17.2), but they are best used when failure is a rare event because
log-linear models do not naturally impose an upper limit of 1 on the risk. For
non-rare failures, we can instead consider a structural nested log-linear model
to model the ratio of cumulative survival probabilities (i.e., 1− risk) under dif-
ferent treatment levels. Structural nested cumulative survival time models doTchetgen Tchetgen et al (2015)
and Robins (1997b) described sur-
vival analysis with instrumental
variables that exhibit similar prob-
lems to those described here for
structural nested models.
precisely that (see Technical Point 17.2), but they are best used when survival
is rare because log-linear models do not naturally impose an upper limit of 1
on the survival. A more general option is to use a structural nested model that
models the ratio of survival times under different treatment options. That is,
an accelerated failure time (AFT) model.
Let T
a
i
be the counterfactual time of survival for individual i under treat-
ment level a. The effect of treatment A on individual i’s survival time can be
measured by the ratio T
a=1
i
/T
a=0
i
of her counterfactual survival times under
treatment and under no treatment. If the survival time ratio is greater than 1,
then treatment is beneficial because it increases the survival time; if the ratio
is less than 1, then treatment is harmful; if the ratio is 1, then treatment has
no effect. Suppose, temporarily, that the effect of treatment is the same for
every individual in the population.
We could then consider the structural nested accelerated failure time (AFT)The “nested” component is only
evident when treatment is time-
varying. See Chapter 21.
model T
a
i
/T
a=0
i
= exp (−ψ
1
a), where ψ
1
measures the expansion (or contrac-
tion) of each individual’s survival time attributable to treatment. If ψ
1
< 0
then treatment increases survival time, if ψ
1
> 0 then treatment decreases
232 Causal survival analysis
Technical Point 17.2
Structural nested cumulative failure time (CFT) models and cumulative survival time (CST) models. For a
time-fixed treatment, a (non-nested) structural CFT model is a model for the ratio of the counterfactual risk under
treatment value a divided by the counterfactual risk under treatment value 0 conditional on treatment A and covariates
L. The general form of the model is
Pr [D
a
k
= 1|L, A]
Pr [D
a=0
k
= 1|L, A]
= exp[γ
k
(L, A; ψ)]
where γ
k
(L, A; ψ) is a function of treatment and covariate history indexed by the (possibly vector-valued) parameter ψ.
For consistency, exp[γ
k
(L, A; ψ)] must be 1 when A = 0 because then the two treatment values being compared are
identical, and when there is no effect of treatment at time m on outcome at time k. An example of such a function is
γ
k
(L, A; ψ) = ψA so ψ = 0 corresponds to no effect, ψ < 0 to beneficial effect, and ψ > 0 to harmful effect.
Analogously, for a time-fixed treatment, a (non-nested) structural CST model is a model for the ratio of the counter-
factual survival under treatment value a divided by the counterfactual survival under treatment level 0 conditional on
treatment A and covariates L. The general form of the model is
Pr [D
a
k
= 0|L, A]
Pr [D
a=0
k
= 0|L, A]
= exp[γ
k
(L, A; ψ)]
Although CFT and CST models differ only in whether we specify a multiplicative model for Pr [D
a
k
= 1|L, A] versus
for Pr [D
a
k
= 0|L, A], the meaning of γ
k
(L, A; ψ) differs because a multiplicative model for risk is not a multiplicative
model for survival, whenever the treatment effect is non-null. When we let the time index k be continuous rather than
discrete, a structural CST model is equivalent to a structural additive hazards model (Tchetgen Tchetgen et al., 2015)
as any model for Pr [D
a
k
= 0|L, A] / Pr
D
a=0
k
= 0|L, A
induces a model for the difference in the time-specific hazards
of T
a
and T
a=0
, and vice-versa.
The use of structural CFT models requires that, for all values of the covariates L, the conditional cumulative probability
of failure under all treatment values satisfies a particular type of rare failure assumption. In this “rare failure” context, the
structural CFT model has an advantage over AFT models: it admits unbiased estimating equations that are differentiable
in the model parameters and thus are easily solved. Page (2005) and Picciotto et al. (2012) provided further details on
structural CFT and CST models. For a time-varying treatment, this class of models can be viewed as a special case of
the multivariate structural nested mean model (Robins 1994). See Technical Point 14.1.
survival time, if ψ
1
= 0 then treatment does not affect survival time. MoreThe negative sign in front of ψ pre-
serves the usual interpretation of
positive parameters indicating harm
and negative parameters indicating
benefit.
generally, the effect of treatment may depend on covariates L so a more general
structural AFT would be T
a
i
/T
a=0
i
= exp (−ψ
1
a − ψ
2
aL
i
), with ψ
1
and ψ
2
(a
vector) constant across individuals. Rearranging the terms, the model can be
written as
T
a=0
i
= T
a
i
exp (ψ
1
a + ψ
2
aL
i
) for all individuals i
Following the same reasoning as in Chapter 14, consistency of counterfactu-
als implies the model T
a=0
i
= T
i
exp (ψ
1
A
i
+ ψ
2
A
i
L
i
), in which the counterfac-
tual time T
a
i
is replaced by the actual survival time T
A
i
= T
i
. The parameters
ψ
1
and ψ
2
can be estimated by a modified g-estimation procedure (to account
for administrative censoring) that we describe later in this section.
The above structural AFT is unrealistic because it is both deterministic
and rank-preserving. It is deterministic because it assumes that, for each in-
dividual, the counterfactual survival time under no treatment T
a=0
can be
computed without error as a function of the observed survival time T , treat-
ment A, and covariates L. It is rank-preserving because, under this model, if
17.6 G-estimation of structural nested models 233
individuals i would die before individual j had they both been untreated, i.e.,
T
a=0
i
< T
a=0
j
, then individual i would also die before individual j had they
both been treated, i.e., T
a=1
i
< T
a=1
j
.
Because of the implausibility of rank preservation, one should not generally
use methods for causal inference that rely on it, as we discussed in Chapter 14.
And yet again we will use a rank-preserving model here to describe g-estimation
for structural AFT models because g-estimation is easier to understand for
rank-preserving models, and because the g-estimation procedure is actually
the same for rank-preserving and non-rank-preserving models.Robins (1997b) described non-
deterministic non-rank-preserving
structural nested AFT models.
Consider the simpler rank-preserving model T
a=0
i
= T
i
exp (ψA
i
) without a
product term between treatment and covariates. G-estimation of the parameter
ψ of this structural AFT model would be straightforward if administrative
censoring did not exist, i.e., if we could observe the time of death T for all
individuals. In fact, in that case the g-estimation procedure would be the
same as we described in Section 14.5. The first step would be to compute
candidate counterfactuals H
i
(ψ
†
) = T
i
exp
ψ
†
A
i
under many possible values
ψ
†
of the causal parameter ψ. The second step would be to find the value ψ
†
Less computationally intensive ap-
proaches, known as directed search
methods, for approximate searching
are available in statistical software.
The Nelder-Mead Simplex method
is an example of a directed search
method.
that results in a H
i
(ψ
†
) that is independent of treatment A in a logistic model
for the probability of A = 1 with H
i
(ψ
†
) and the confounders L as covariates.
Such value ψ
†
would be the g-estimate of ψ.
However, this procedure cannot be implemented in the presence of admin-
istrative censoring at time K because H
i
(ψ
†
) cannot be computed for individ-
uals with unknown T
i
. One might then be tempted to restrict the g-estimation
procedure to individuals with an observed survival time only, i.e., those with
T
i
≤ K. Unfortunately, that approach results in selection bias. To see why,
consider the following oversimplified scenario.
We conduct a 60-month randomized experiment to estimate the effect of
a dichotomous treatment A on survival time T . Only 3 types of individuals
participate in our study. Type 1 individuals are those who, in the absence of
treatment, would die at 36 months (T
a=0
= 36). Type 2 individuals are those
who in the absence of treatment, would die at 72 months (T
a=0
= 72). Type 3
individuals are those who in the absence of treatment, would die at 108 months
(T
a=0
= 108). That is, type 3 individuals have the best prognosis and type
1 individuals have the worst one. Because of randomization, we expect that
Type
1 2 3
T
a=0
36 72 108
T
a=1
24 48 72
Table 17.1
the proportions of type 1, type 2, and type 3 individuals are the same in each
of the two treatment groups A = 1 and A = 0. That is, the treated and the
untreated are expected to be exchangeable.
Suppose that treatment A = 1 decreases the survival time compared with
A = 0. Table 17.1 shows the survival time under treatment and under no treat-
ment for each type of individual. Because the administrative end of follow-up is
K = 60 months, the death of type 1 individuals will be observed whether they
are randomly assigned to A = 1 or A = 0 (both survival times are less than 60),
and the death of type 3 individuals will be administratively censored whether
they are randomly assigned to A = 1 or A = 0 (both survival times are greater
than 60). The death of type 2 individuals, however, will only be observed if
they are assigned to A = 1. Hence an analysis that welcomes all individuals
with non-administratively censored death times will have an imbalance of in-
dividual types between the treated and the untreated. Exchangeability will be
broken because the A = 1 group will include type 1 and type 2 individuals,
whereas the A = 0 group will include type 1 individuals only. Individuals in the
A = 0 group will have, on average, a worse prognosis than those in the A = 1
group, which will make treatment look better than it really is. This selection
bias (Chapter 8) arises when treatment has a non-null effect on survival time.
234 Causal survival analysis
Technical Point 17.3
Artificial censoring Let K(ψ) be the minimum survival time under no treatment that could possibly correspond
to an individual who actually died at time K (the administrative end of follow-up). For a dichotomous treatment
A, K(ψ) = inf {K exp (ψA)}, which implies that K(ψ) = K exp (ψ × 0) = K if treatment contracts the survival
time (i.e., ψ > 0), K(ψ) = K exp (ψ × 1) = K exp (ψ) if treatment expands the survival time (i.e., ψ < 0), and
K(ψ) = K exp (0) = K if treatment does not affect survival time (i.e., ψ = 0).
All individuals who are administratively censored (i.e., T > K) have ∆(ψ) = 0 because there is at least one treatment
level (the one they actually received) under which their survival time is greater than K, i.e., H(ψ) ≥ K(ψ). Some of
the individuals who are not administratively censored (i.e., T ≤ K) also have ∆(ψ) = 0 and are excluded from the
analysis—they are artificially censored—to avoid selection bias.
The artificial censoring indicator ∆(ψ) is a function of H(ψ) and K. Under conditional exchangeability given L, all
such functions, when evaluated at the true value of ψ, are conditionally independent of treatment A given the covariates
L. That is, g-estimation of the AFT model parameters can be performed based on ∆(ψ) rather than H(ψ). Technically,
∆(ψ) is substituted for H(ψ) in the estimating equation of Technical Point 14.2. For practical estimation details, see
the Appendix of Hern´an et al (2005).
To avoid this selection bias, one needs to select individuals whose survival
time would have been observed by the end of follow-up whether they had
been treated or untreated, i.e., those with T
a=0
i
≤ K and T
a=1
i
≤ K. In our
example, we will have to exclude all type 2 individuals from the analysis in order
to preserve exchangeability. That is, we will not only exclude administratively
censored individuals with T
i
> K, but also some uncensored individuals withThis exclusion of uncensored indi-
viduals from the analysis is often re-
ferred to as artificial censoring. See
Technical Point 17.3.
known survival time T
i
≤ K because their survival time would have been
greater than K if they had received a treatment level different from the one
they actually received.
We then define an indicator ∆(ψ), which takes value 0 when an individual
is excluded and 1 when she is not. The g-estimation procedure is then modified
by replacing the variable H(ψ
†
) by the indicator ∆(ψ
†
). See Technical Point
17.3 for details. In our example, the g-estimate
ˆ
ψ from the rank-preserving
structural AFT model T
a=0
i
= T
i
exp (ψA
i
) was −0.047 (95% confidence inter-Code: Program 17.5
The point estimate of ψ is the
value that corresponds to the min-
imum of the estimating function
described in Technical Point 17.3.;
the limits of the 95% confidence
interval are the values that corre-
spond to the value 3.84 (χ
2
with
one degree of freedom) of the esti-
mating function.
val: −0.223 to 0.333). The number exp
−
ˆ
ψ
= 1.05 can be interpreted as the
median survival time that would have been observed if all individuals in the
study had received a = 1 divided by the median survival time that would have
been observed if all individuals in the study had received a = 0. This survival
time ratio suggests little effect of smoking cessation A on the time to death.
As we said in Chapter 14, structural nested models, including AFT models,
have rarely been used in practice. A practical obstacle for the implementation
of the method is the lack of user-friendly software. An even more serious
obstacle in the survival analysis setting is that the parameters of structural
AFT models need to be estimated through search algorithms that are not
guaranteed to find a unique solution. This problem is exacerbated for models
with two or more parameters ψ. As a result, the few published applications
of this method tend to use simplistic AFT models that do not allow for the
treatment effect to vary across covariate values.
This state of affairs is unfortunate because subject-matter knowledge (e.g.,
biological mechanisms) is easier to translate into parameters of structural AFT
models than into those of structural hazards models. This is especially true
when using non-deterministic and non-rank preserving structural AFT models.
Chapter 18
VARIABLE SELECTION AND HIGH-DIMENSIONAL DATA
In the previous chapters, we have described several adjustment methods to estimate the causal effect of a treatment
A on an outcome Y , including stratification and outcome regression, standardization and the parametric g-formula,
IP weighting, and g-estimation. Each of these methods carry out the adjustment in different ways but all these
methods rely on the same condition: the set of adjustment variables L must include sufficient information to
achieve conditional exchangeability between the treated A = 1 and the untreated A = 0—or, equivalently, to block
all backdoor paths between A and Y without opening other biasing paths.
In practice, a common question is how to select the variables L for adjustment. This chapter offers some guidelines
for variable selection when the goal of the data analysis is causal inference. Because the variable selection criteria
for causal inference are not the same as for prediction, widespread procedures for variable selection in predictive
analyses may not be directly transferable to causal analyses. This chapter summarizes the problems of incorrect
variable selection in causal analyses and outlines some practical guidance.
18.1 The different goals of variable selection
As we have discussed throughout this book, valid causal inferences usually
require adjustment for confounding and other biases. When an association
measure between a treatment A and an outcome Y may be partly or fully
explained by confounders L, adjustment for these confounders needs to be
incorporated into the data analysis. Otherwise, the association measure cannot
be interpreted as a causal effect measure.Even if the outcome model includes
all confounders for the effect of
A on Y , the association between
each confounder and the outcome
cannot be causally interpreted be-
cause we do not adjust for the con-
founders of the confounders.
But if the goal of the data analysis is purely predictive, no adjustment for
confounding is necessary. If we just want to quantify the association between
smoking cessation A and weight gain Y , we simply estimate that association
from the data by comparing the average weight gain between those who did and
did not quit smoking. More generally, if we want to develop a predictive model
for weight gain, we will want to include covariates (like smoking cessation,
baseline weight, and annual income) that predict weight gain. We do not
ask the question of whether those covariates are confounders because there is
no treatment variable whose effect can be confounded. In predictive models,
we do not try to endow any parameter estimates with a causal interpretation
and therefore we do not try to adjust for confounding because the concept ofReminder: Confounding is a causal
concept that does not apply when
the estimand is an association
rather than a causal effect.
confounding does not even apply.
The distinction between predictive/associational models and causal models
was discussed in Section 15.5. Suppose clinical investigators use outcome re-
gression to identify patients at high risk of developing heart failure. The goal is
classification, which is a form of prediction. The parameters of these predictive
models do not necessarily have any causal interpretation and all covariates in
the model have the same status, i.e., there are no treatment variable A and
adjustment variables L. For example, a prior hospitalization may be identified
as a useful predictor of future heart failure, but nobody would suggest we stop
admitting people to the hospital in order to prevent heart failures. Identifying
236 Variable selection and high-dimensional data
patients with bad prognosis (prediction) is different from identifying the best
course of action to prevent or treat a disease (causal inference).
For pure prediction, investigators want to use variables that improve pre-
dictive ability. Most prediction algorithms include so-called tuning parameters
whose values must chosen in order to optimize predictive accuracy. For in-
stance, the lasso and ridge regression both include a regularization parameter
than shrinks regression coefficients towards zero. However the appropriate de-
gree of shrinkage (i.e., the magnitude of the regularization parameter) needs
to be adaptively chosen from the data. For neural nets the tuning parameters
include the depth and width of the network. Often the choice of tuning pa-
rameter is made using cross-validation (see Fine Point 18.2). Cross-validation
is also used to choose between competing algorithms as no single algorithm
gives better predictions than the others in all data sets.
Because some selection algorithms such as deep neural nets are “black-box”
procedures, it is not always easy to explain how the variables are selected or
why the algorithms works. One point of view is that it does not necessarily
matter; that is, for purely predictive purposes in a particular population and
setting, whatever algorithm that works to improve prediction is fair game,
regardless of interpretability.
Another point of view is that interpretable algorithms are needed because
physicians will not feel comfortable in their treatment decisions, especially for
patients with an unusual mixture of symptoms, if they cannot articulate to
themselves and the patient the medical reasons behind these decisions. Fur-
thermore, black-box algorithms may perform poorly when deployed to new
settings because they are likely to rely on local, often noncausal, features of
the training setting that are not present in the new settings. Finally, black-box
algorithms can bake in often predictive, but nonetheless (socially) discrimina-
tory, practices because the training set data were collected when those practices
were in place.
A causal analysis requires different considerations. Unlike in a predictive
analysis, in a causal analysis a thoughtful selection of confounders is needed
if one is to believe the treatment effect estimates have a causal interpretation.
Automatic variable selection procedures may work for prediction, but not gen-
erally for causal inference. Variable selection algorithms may select variables
for adjustment that introduce bias in the effect estimate. There are several
reasons why this bias may arise. Some of these reasons have been described
earlier in the book; others have not been described yet. The next section
summarizes all of them.
18.2 Variables that induce or amplify bias
Imagine that we have unlimited computational power and a dataset with a
quasi-infinite number of individuals (the rows of the dataset) and many vari-
Figure 18.1
ables measured for each individual (the columns of the data set), including
treatment A, outcome Y , and a moderate number of discrete variables X, some
of which may be confounders of the effect of A on Y . In this setting, we can
afford to adjust for as many variables in the dataset as we wish, without com-
putational, numerical, or statistical constraints. Thus, were our goal simply to
predict Y from A and X (under a standard least squares loss; see Technical
Point 18.1), we could optimally predict Y by simply using the average of Y in
every joint stratum of A and X.
18.2 Variables that induce or amplify bias 237
Fine Point 18.1
Variable selection procedures for regression models Suppose we want to fit a regression model with predictive
purposes, but the database includes so many potential predictors—perhaps even more than individuals—that including
all of them in the model is either impossible or results in very unstable predictions. Several approaches exist to deal
with this problem in regression models. A detailed description of these procedures can be found in many books. See,
e.g., the books by Hastie, Tibshirani, and Friedman (2009), and by Harrell (2015). Below we briefly outline some of the
existing approaches.
One approach is to select a subset of the available variables. A conceptually simple way to find the best subset
would be to first decide the number of variables in the model, then fit all possible combinations of models with that
number of variables, and finally choose the best one according to some pre-specified criterion (e.g., Akaike’s Information
criterion). However, this approach becomes computationally infeasible for a massive number of variables and, for a finite
dataset, is not guaranteed to select the model with smallest prediction error. More computationally efficient methods
to select variables are forward selection (start with no variables and, in each step of the algorithm, add the variable that
leads to the greatest improvement), backward elimination (start with all variables and, in each step, delete the variable
that leads to the smallest improvement), and stepwise selection (a combination of forward selection and backward
elimination). The variable selection algorithm ends when no further improvement is possible, with improvement again
defined according to some pre-specified criterion. These algorithms are easy to implement but, on the other hand, they
do not explore all possible subsets of variables.
An alternative to subset selection is shrinkage. The idea is to modify the estimation method by adding a “penalty”
that forces the model parameter estimates (other than the intercept) to be closer to zero than they would have been in
the absence of the penalty. That is, most parameter estimates are shrunk towards zero. As a result of this shrinkage, the
variance decreases and the prediction becomes more stable. The two best known shrinkage methods are ridge regression
and the lasso or “least absolute shrinkage and selection operator”, which was proposed by Santosa and Symes (1986)
and rediscovered by Tibshirani (1996). Unlike ridge regression, the lasso allows some parameter values to be exactly
zero. Therefore, the lasso is both a shrinkage method and a subset selection method.
However, suppose we want to unbiasedly estimate the average causal ef-
fect of a binary treatment A on the outcome Y , i.e., E
Y
a=1
− E
Y
a=0
.
Then the goal of covariate adjustment is to eliminate as much confounding as
possible by using the information contained in the measured variables X. We
could easily adjust for all measured variables X via stratification/outcome re-Collapsibility reminder: When ad-
justing for covariates using strat-
ification, remember that the ad-
justed association measure may dif-
fer from the unadjusted association
measure, even when no confound-
ing exists. See Fine Point 4.3.
gression, standardization/g-formula, IP weighting, or g-estimation. Are there
any reasons to adjust for only a subset of X rather than simply adjust for all
available variables X? The answer is yes. Even in this ideal setting, we want to
ensure that some variables are not selected for adjustment because adjustment
for those variables would induce bias. The next examples illustrate this point
when some of the variables L in X are causally affected by A.
Suppose the causal structure of the problem is represented by the causal
diagram of Figure 18.1 (same as Figure 7.7) in which the variable L is a collider.
Here the average causal effect E[Y
a=1
] − E[Y
a=0
] = 0 is unbiasedly estimated
by E [Y |A = 1] − E [Y |A = 0] since there is no confounding by L. Suppose
now we try to estimate the average causal effect by adjusting for L via the
g-formula
P
l
E [Y |A = 1, L = l] Pr (L = l) −
P
l
E [Y |A = 0, L = l] Pr (L = l).
This contrast differs from E [Y |A = 1] − E [Y |A = 0]—and thus is biased—
because L is both conditionally associated with Y given A and marginally
associated with A, so Pr (L = l) = Pr (L = l|A). Because the A-Y association
adjusted for L is expected to be non-null even though the causal effect of
treatment A on the outcome Y is null, we say that there is selection bias under
the null. The same bias is expected to arise when we adjust for a variable L
238 Variable selection and high-dimensional data
Fine Point 18.2
Overfitting and cross-validation. Overfitting is a common problem of all variable selection methods for regression
models: The variables are selected to predict the data points as well as possible, without taking in consideration that
some of the variation observed in the data is purely random. As a result, the model predicts very well for the individuals
used to estimate the model parameters, but the model predicts poorly for future individuals who were not used to estimate
the model parameters. The same problem arises in predictive algorithms such as random forests, neural networks, and
other machine learning algorithms.
A straightforward solution to the overfitting problem is to split the sample in two parts: a training sample used to
run the predictive algorithm (that is, to estimate the model parameters when using regression) and a validation sample
used to evaluate the accuracy of the algorithm’s predictions. For a sample size n, we use v individuals for the validation
set and n −v individuals for the training set. When using the lasso, the degree of shrinkage in the training sample may
be guided by the model’s performance in the validation sample.
The obvious downside of splitting the sample into training and validation subsamples is that the predictive algorithm
only uses—e.g., the model parameters are estimated in—a subset of individuals, which increases the variance. A solution
is to repeat the splitting process multiple times, which increases the effective number of individuals used by the predictive
algorithm. Then one can evaluate the algorithm’s predictive accuracy as the average over all the validation samples.
This procedure is known as cross-validation or out-of-sample testing. Different forms of cross-validation exist.
A procedure referred to as “leave-v-out cross-validation” analyzes all possible partitions of the sample into training
sample and validation sample of size v. However, examining all such partitions may become computationally infeasible
for moderately large values of n and v. Two possible fixes for this problem are (i) to choose v = 1 or (ii) to evaluate
only a sample of the partitions. For example, in “k-fold cross validation”, the sample is split into k subsamples of equal
size. Then each one of the subsamples is used as the validation sample with the other k − 1 subsamples as its training
sample. A common choice is k = 10. See the book by Hastie, Tibshirani, and Friedman (2009) for a description of
cross-validation and related techniques Deep learning algorithms based on neural networks with many layers often
seem nearly immune to overfitting when massive amounts of training data are available, e.g., speech recognition, images
(Goodfellow, Bengio, Courville 2016). A deep neural network is a parametric model with often thousands, millions, or
even billions unknown parameters and therefore often fits the training data exactly. Astonishingly, the fitted model still
can successfully predict the outcomes of future individuals (sampled from the same population) with small error. Trying
to explain this phenomenon is one of the most active current research areas in machine learning.
that, as in the causal diagram of Figure 18.2, is a descendant of the collider
Figure 18.2
B. You may want to review Chapter 8 for more examples of causal structures
with colliders and their descendants.
Selection bias may also appear when adjusting for a noncollider affected
by treatment, like the variable L in the causal diagram in Figure 18.3. Here
the average causal effect E[Y
a=1
] − E[Y
a=0
] = 0 is also unbiasedly estimated
by E [Y |A = 1] − E [Y |A = 0] since there is no confounding by L. However, if
we try to estimate the average causal effect by adjusting for L (as if it were a
pre-treatment variable), the g-formula contrast will differ from E [Y |A = 1] −
E [Y |A = 0] for the same reasons as in the previous paragraph.
Now suppose that the arrow from A to Y had been absent, i.e., that the
null hypothesis of no effect of A on Y were true and so E[Y
a=1
] −E[Y
a=0
] = 0.
Then A and Y would be independent (both marginally and conditionally on L)
and the g-formula contrast would be zero and thus unbiased. The key reason
for this result is that, under the null, A no longer has a causal effect on L.
Figure 18.3 That is, unlike in Figures 18.1 and 18.2, adjusting for L in Figure 18.3 results
in selection bias only when A has a non-null causal effect on Y . We then say
that there is selection bias under the alternative or off the null (see Section
6.5).
18.2 Variables that induce or amplify bias 239
When the adjustment variable is affected by the treatment A and affects
the outcome Y , we say that the variable is a mediator. Consider the causal
diagram in Figure 18.4, which includes the mediator L on a causal path from
Figure 18.4 the treatment A to the outcome Y . The A-Y association adjusted for the
mediator L, or its descendants, will differ from the effect of treatment A on
the outcome Y because the adjustment blocks the component of the effect that
goes through L. Sometimes this problem is referred to as overadjustment forIn Figure 18.4, adjusting for L
blocks the path A → L → Y but
not the path A → Y . Thus the
A-Y association adjusted for L is a
biased estimator of the total effect
of A on Y but an unbiased estima-
tor of the direct effect of A on Y
that is not mediated through L.
mediators when the average causal effect of A on Y is the contrast of interest.
The bias-inducing variables discussed above share a common feature: they
are affected by treatment and therefore they are post-treatment variables. One
might then think that we should always avoid adjustment for variables that
occur after treatment A. The rule of not adjusting for post-treatment variables
would be easy to follow because the temporal sequence of the adjustment
variables and the treatment is usually known. Unfortunately, following this
simple rule may result in the exclusion of useful adjustment variables, as we
discussed in Fine Point 7.4. Consider the causal diagram in Figure 18.5. The
variable L is a post-treatment variable, but it can be used to block the backdoor
path between treatment A and outcome Y . Therefore, the A-Y association
adjusted for L is an unbiased estimator of the effect of A on Y , whereas the
unadjusted A-Y association is a biased estimator. The take home message is
that causal graphs do not care about temporal order. Thus, when A does not
affect L, the correct analysis must be the same whether L is temporally before
or temporally after A.
The problem is that, even when we know the temporal order of the vari-
Figure 18.5 ables, we cannot determine from the data whether or not A affects L. In fact,
given the temporal ordering A L Y , any joint distribution of (A, L, Y ) without
any independencies is compatible with several causal graphs. So the decision
whether to adjust for L must be based on information outside of the data.
That is, whether to adjust for L cannot be determined via any automated
procedures that rely exclusively on statistical associations. For example, as
discussed in Chapter 7, there is no way to distinguish a collider from a con-
founder by using data only. Rather, the exclusion of bias-inducing variablesAn example of the application of
expert knowledge to adjustment
was described by Hern´an et al
(2002).
from the adjustment set needs to be guided by subject-matter knowledge about
the causal structure of the problem.
We next turn to the question of adjustment for variables L that are tempo-
rally prior to treatment A, i.e., our temporal ordering is now L A Y . Suppose,
for simplicity, that the sample size is very large, greatly exceeding the num-
ber of covariates X available for adjustment. As a consequence, the variance
of any estimator will be negligible and the only issue is bias. In this setting
it is commonly believed that an estimator that adjusts for all available pre-
treatment covariates will minimize the bias. However, this belief is wrong for
two separate reasons.
Consider the causal diagram of Figure 18.6 (same as Figure 7.4), which
includes a pre-treatment variable L. Because L is a collider on a path from
A to Y , adjusting for it will introduce selection bias, which we referred to as
M-bias in Chapter 7. Again, the observed data cannot distinguish between
Figure 18.6 confounders and colliders, so one must rely on whatever external information
one may have to decide whether or not to adjust for a pre-treatment variable L.
In fact, it is also possible that L is both a confounder and a collider—if there
were an arrow from L to A in Figure 18.6—which implies that the average
causal effect cannot be identified, regardless of whether we do or do not adjust
for L.
There is one additional reason to avoid indiscriminate adjustment for pre-
240 Variable selection and high-dimensional data
treatment variables: bias amplification, a phenomenon we have not yet de-
scribed in this book. Consider the causal diagram of Figure 18.7 (same as
Figure 16.1), which represents a setting in which the causal effect of treatment
A on the outcome Y is confounded by the unmeasured variable U. Because
U is not available in the data, we cannot adjust for U and the confounding
is intractable. Adjustment for the variable Z—using the g-formula as above
with L replaced by Z—does not eliminate confounding because Z is not on
Figure 18.7 any backdoor path from the treatment A to the outcome Y . In fact, Z is an
instrument—which can be used for instrumental variable estimation in some
situations described in Chapter 16—and therefore useless for direct confound-
ing adjustment by the g-formula.
Interestingly, even though Z cannot be used to adjust away the confounding
bias due to U, adjustment for the instrument Z can amplify the confounding
bias due to U. That is, the A-Y association adjusted for Z may be further from
the effect of A on Y than the A-Y association not adjusted for Z. This biasBias amplification is guaranteed
if all the equations in the struc-
tural equation model correspond-
ing to the causal diagram are lin-
ear (Wooldridge 2010, Pearl 2011),
but may also occur in more realistic
settings (Ding et al. 2017).
amplification due to adjusting for an instrument Z, often referred to as Z-bias,
is a reason to avoid adjustment for variables that, like Z, are instruments. Bias
amplification, however, is not guaranteed: adjustment for Z could also reduce
the bias due to confounding by the unmeasured variable U. Generally, it is not
possible to know whether adjustment for an instrument will amplify or reduce
bias.
In summary, even if we had no computational constraints and a quasi-
infinite sample size, it is not advisable to adjust for all available variables X.
Ideally, the adjustment set would not include any variables that may introduce
or amplify bias. Because these bias-inducing variables cannot be empirically
identified by purely statistical algorithms, expert knowledge is needed to guide
variable selection.
18.3 Causal inference and machine learning
For the remainder of this chapter, we will assume that we have somehow suc-
ceeded at ensuring that X includes no variables that may induce or amplify
bias (i.e., no variables that would destroy conditional exchangeability if ad-
justed for) while still including all confounders L of the average causal ef-
fect of A on Y (i.e., all variables needed to achieve conditional exchangeabil-
ity).Furthermore, we assume positivity holds. Our next problem is to estimate
this effect E
Y
a=1
− E
Y
a=0
in practice when X is very high-dimensional
or includes multiple continuous variables.
If we have good estimates of E
Y
a=1
and E
Y
a=0
, their difference will
be a good estimate of E
Y
a=1
−E
Y
a=0
. Thus, for simplicity, we will focus
on the estimation of E
Y
a=1
.
Depending on the adjustment method that we choose, the variables X will
be used in different ways. When using the plug-in g-formula (standardization)
to estimate E
Y
a=1
, we will estimate the mean outcome Y conditional on the
variables X among individuals with A = 1, which we refer to as b(X); when
using IP weighting, we will estimate the probability of treatment A conditional
on the variables X, which we refer to as π(X). We can produce estimates
ˆ
b(x)
and ˆπ(x) via the sort of traditional parametric models (e.g., generalized linear
models with linear, logistic, or log links) with the number of parameters much
smaller than the sample size that we have described in Part II of this book.
When X is high-dimensional, such models are certain to be misspecified. As
18.4 Doubly robust machine learning estimators 241
a consequence, both
ˆ
b(x) and ˆπ(x) will fail to be consistent for the true b(x)
and π(x).
To reduce the possibility of model misspecification, we might want to fit
richly parameterized generalized linear models with linear predictor θ
T
s (x) =
P
j
θ
j
s
j
(x), where s (X) is a very high-dimensional vector of transformations
of the covariate vector X. The vector s (X) generally contains both flexi-
ble high-dimensional transformations (e.g., cubic splines) of individual vari-
ables in X and cross-variable products of these transformations. For concrete-
ness, suppose we choose a logit link so
ˆ
b(x) = expit
b
θ
T
b
s (x)
and ˆπ(x) =
expit
b
θ
T
π
s (x)
where θ
b
and θ
π
are the parameters of the models for b(x) and
π(x). Even if the estimated functions
ˆ
b(x) and ˆπ(x) based on these models
are consistent, in finite samples the errors
ˆ
b(x) −b (x) and ˆπ(x) −π(x) will be
much greater than would be the case for a correctly specified low-dimensional
parametric model. In fact the dimension of s (X) may frequently exceed the
number of individuals n contributing data to the study. In that case, a fit of
the model will fail to converge and no estimate of θ will be returned.Remember that some of the vari-
ables in X may not even be con-
founders so we would not need to
adjust for them if we knew which
variables they were.
Possible ways forward are to fit the parametric model with linear predic-
tor θ
T
s (X) by adding a lasso or ridge penalty (see Fine Point 18.1), to use
a variable selection algorithm such as stepwise selection, or to estimate the
conditional expectations b(X) and π(X) using other predictive machine learn-
ing algorithms such as tree-based algorithms (e.g., random forests) or neural
networks (e.g., deep learning). As discussed in Fine Point 18.2, deep learning
algorithms fit a model often containing thousands or millions of parameters.
Other machine learning algorithms also effectively fit thousands of parame-Machine learning algorithms can
use cross-validation (see Fine Point
18.2) to optimize predictive accu-
racy.
ters. In most cases with large sample sizes and many covariates X, machine
learning algorithms outperform traditional parametric models for the accurate
prediction of conditional expectations.
However, predictive machine learning algorithms do not by themselves suf-
fice to adequately adjust for confounding in high-dimensional settings. In the
next section we explain that these algorithms must be used in conjunction with
doubly robust estimators with two modifications: sample splitting and cross-
fitting. This is necessary if we hope to construct valid 95% Wald confidence
intervals, i.e., intervals that trap the causal parameter of interest at least 95%
of the time.
18.4 Doubly robust machine learning estimators
Valid Wald intervals for ψ = E
Y
a=1
require that the bias of the estimator
be much less than the standard error of the estimator. The standard error of
most estimators
b
E
Y
a=1
of E
Y
a=1
scale as 1/
√
n times a constant, where
n is the sample size. Hence, we require that the bias of
b
E
Y
a=1
to be much
less than 1/
√
n. In addition to small bias, in order to have valid Wald intervalsThe degree of undercoverage will
be greater when there is some de-
gree of confounding in the super-
population since, in that case, Wald
confidence intervals will not be cen-
tered on an unbiased estimator of
the causal effect (see Chapter 10).
centered on
b
E
Y
a=1
, we generally need
b
E
Y
a=1
to also be asymptotically
normal, which is generally easier to achieve than small bias.
A small bias is easier to achieve with doubly robust estimators than with
non-doubly robust estimators, because the bias
b
E
Y
a=1
−E
Y
a=1
of a dou-
bly robust estimator depends on the product of the errors
1
π(x)
−
1
ˆπ(x)
and
b(x) −
ˆ
b(x), which can be small. Indeed the bias is less than 1/
√
n if both
errors are much smaller than 1/
4
√
n, which can often be achieved by machine
242 Variable selection and high-dimensional data
learning estimators if the functions π(x) and b(x) are either quite smooth, i.e.,
have many derivatives, or very sparse, i.e., depend on only few components
of the vector X, even though how many and which components are unknown.This property of doubly robust esti-
mators is referred to as a second-
order bias. See Technical Point
13.2 for details.
In contrast, the IP weighted and plug-in g-formula estimators of E
Y
a=1
can
have bias as large as the errors
1
π(x)
−
1
ˆπ(x)
and b(x) −
ˆ
b(x), respectively. If
so, neither the IP weighted estimator nor the plug-in g-formula estimator of
E
Y
a=1
can generally center a valid Wald confidence interval because, with
high-dimensional X, it is known that the error of any possible estimator ˆπ(x)
or
ˆ
b(x) of π(x) or b(x) must exceed 1/
√
n.
But, if we hope to construct valid 95% Wald confidence intervals, the doubly
robust machine learning estimators of the previous paragraph need to incorpo-
rate sample splitting and cross-fitting. We now describe these two procedures
and their rationale. Technical Point 18.1 summarizes the steps of the estima-
tion process.
We begin by describing sample splitting. First, we randomly divide the
study population of n individuals into two halves: an estimation sample of size
n/2 and a training sample of equal size. Second, we apply the predictive ma-We may refer to the training sample
as the nuisance sample because we
use it to estimate the nuisance re-
gressions for b(X) and π(X). Fine
Point 15.1 reviews the concept of
nuisance parameters.
chine learning algorithms to the training sample in order to obtain estimators
of
ˆ
b(x) and ˆπ(x) for the conditional expectations b (x) = E[Y |X = x, A = 1]
and π (x) = E[A|X = x], respectively. Third, we compute the doubly robust
estimator of the average causal effect in the estimation sample using the es-
timators of
ˆ
b(x) and ˆπ(x) from the training sample. We have now obtained
a doubly robust machine learning estimate of the average causal effect in a
random half of the study population.
To understand the need for sample splitting, let us compare the split-sample
version with the full-sample version of the augmented IP weighted (AIPW)
doubly robust estimator of Technical Point 13.2. The estimation sample used
in the split-sample AIPW estimator of E
Y
a=1
is statistically independent
of the split-sample estimators of
b
b (x) and bπ (x), which use only the training
sample data. As a consequence, under weak conditions described in Technical
Point 18.2, the estimator is asymptotically normal with standard error that
scales like 1/
√
n with the product bias described ealier. It follows that, if the
product bias is less than 1/
√
n, Wald intervals centered on the split-sample
estimator will be valid.
In contrast, the full-sample AIPW estimator of E
Y
a=1
is
1
n
n
X
i=1
b
b (X
i
) +
A
i
bπ (X
i
)
n
Y
i
−
b
b (X
i
)
o
,
where
b
b (x) and bπ (x) are now estimated by a machine learning algorithm ap-
plied to all n individuals’ data. Thus
b
b (x) and bπ (x) are correlated with the
full-sample AIPW estimator. This correlation, if sufficiently large, can affect
the bias, variance, and asymptotic normality of the full-sample estimator in
unpredictable ways. Unfortunately, the magnitude of the correlation is un-
known and cannot be well estimated. Hence, the split-sample estimator is
much preferred to the full-sample estimator in high-dimensional settings.Sample splitting and cross-fitting
are not new procedures. However,
the idea of combining these proce-
dures with machine learning has not
been emphasized until recently.
The only difficulty with using the doubly robust split-sample estimator is
that its variance and standard error correspond to a sample size of n/2. As
a result, our confidence interval will be wider than the one we would have
obtained if we had been able to use the entire sample of n individuals. A way
to overcome this problem is cross-fitting.
We now describe how cross-fitting recovers the statistical efficiency lost by
sample splitting. First, we repeat the above procedure but swapping the roles
18.4 Doubly robust machine learning estimators 243
Technical Point 18.1
Augmented IP weighted split-sample and cross-fit estimator. The augmented IP weighted (AIPW) estimator of
ψ = E
Y
a=1
is a doubly robust estimator described in Technical Point 13.2. The following algorithm computes the
AIPW split-sample estimator
b
ψ and the cross-fit estimator
b
ψ
cross-fit
:
(i) Randomly split the n study subjects into 2 parts: an estimation sample of size q and a training sample of size
n
tr
= n − q with q/n ≈ 1/2.
(ii) Estimate
b
b (x) and bπ (x) of b (x) = E[Y |A = 1, X = x] and π (x) = pr[A = 1| X = x] from the training sample
data using machine learning algorithms.
(iii) Compute the split-sample AIPW estimator
b
ψ =
1
q
q
X
i=1
b
b (X
i
) +
A
i
bπ (X
i
)
n
Y
i
−
b
b (X
i
)
o
from the q subjects in the estimation sample.
(iv) Compute the cross-fit estimator
b
ψ
cross-fit
=
b
ψ +
b
ψ
/2
where
b
ψ is
b
ψ but with the training and estimation sample swapped.
An alternative cross-fit estimator with improved finite sample behavior is computed as follows: (i) divide the sample
of size n into M > 2 equal-sized random samples, (ii) compute
b
ψ
(m)
, m = 1, 2, . . . , M, using sample m as estimation
sample and the remaining M − 1 samples as the training sample, and (iii) compute
b
ψ
cross-fit
=
1
M
P
M
m=1
b
ψ
(m)
.
of the estimation and training halves of the study population. That is, we
use the half formerly reserved for estimation as the new training sample, and
the half formerly used for training as the new estimation sample. We then
compute the doubly robust estimator of the average causal effect in the new
estimation sample using the estimators of
ˆ
b(x) and ˆπ(x) from the new training
sample. We have now obtained a doubly robust machine learning estimate of
the average causal effect in the other random half of the population.
The next step is to compute the average of the two doubly robust estimates
from each half of the population. This average will be our doubly robust
estimate of the effect in the entire study population. A 95% confidence interval
around this estimate can be constructed by bootstrapping, either by adding
and subtracting 1.96 times the bootstrap standard error or by using the 2.5
and 97.5 percentiles of the bootstrap estimates as the bounds of the interval.
We are done. Through sample splitting and cross-fitting, we can combine
doubly robust estimation and machine learning to obtain causal effect estimates
which have known statistical properties and which use all the available data.Lin et al. (2020) constructed esti-
mators based on higher order influ-
ence functions that had smaller bias
than doubly robust cross-fit estima-
tors without significantly increasing
their variance.
An active area of research is the development of procedures to detect whether
the bias of doubly robust split-sample estimators is the order of or larger than
the standard error and, if so, to obtain estimates with smaller bias in the
estimation sample without having to redo the machine learning component in
the training sample.
244 Variable selection and high-dimensional data
Technical Point 18.2
Statistical properties of split-sample and cross-fit estimators. Conditional on the training sample data T
r
,
b
b (x)
and bπ (x) are fixed functions. Hence
b
ψ is the sum of independent and identically distributed random variables and thus,
by the central limit theorem, it is asymptotically normal conditional on T
r
with standard error se
b
ψ
proportional to
n
−1/2
. The exact conditional bias of
b
ψ is
E
h
b
ψ − ψ|T
r
i
= E
π (X
i
)
1
bπ (X
i
)
−
1
π (X
i
)
n
b (X) −
b
b (X)
o
|T r
To characterize the unconditional statistical properties of
b
ψ and
b
ψ
cross-fit
, we must take into account that E
h
b
ψ − ψ|T
r
i
is random through its dependence on the training sample data via
ˆ
b and bπ. If (i)
b
b (x) and bπ (x) are consistent for the
true b (x) and π (x) (in mean square), and (ii) E
h
b
ψ − ψ|T
r
i
/se
b
ψ
converges to 0 in probability, then
b
ψ and
b
ψ
cross-fit
are asymptotically normal and unbiased.
Thus, when (i) and (ii) hold, 95% Wald confidence intervals
b
ψ ± 1.96 ×
b
se
b
ψ
and
b
ψ
cross-fit
± 1.96 ×
b
se
b
ψ
cross-fit
are valid and, in fact, are calibrated. Here bse
b
ψ
cross-fit
and bse
b
ψ
can be computed with the bootstrap. Further,
n
1/2
bse
b
ψ
cross-fit
is semiparametric efficient with standard error
n
var
n
b (X) +
A
π(X)
[Y − b (X)]
oo
1/2
, which is smaller
than the standard error of
b
ψ by a factor of 1/
√
2. Note if the rate of convergence of
1
bπ(x)
−
1
π(x)
is n
−α
and that of
b (x) −
b
b (x) is n
−ϵ
, the bias E
h
b
ψ − ψ|T
r
i
is o
n
−1/2
if α + ϵ > 1/2. Thus if
b
b (x) has a rate of convergence slower
than n
−1/4
, the bias can still be o
n
−1/2
if bπ (x) has a sufficiently fast rate of convergence. The same holds with the
roles of
b
b (x) and bπ (x) swapped.
18.5 Variable selection is a difficult problem
The methods outlined in the previous section invalidate the widespread belief
that any data-adaptive procedure to select adjustment variables will inevitably
result in incorrect confidence intervals. As we have seen, the combination
of causal inference methods with machine learning algorithms for confounder
selection can, under certain conditions, result in correct statistical inference.
However, doubly robust machine learning does not solve all our problems for
at least three reasons (in addition to that described in the previous section).
First, in many applications, the available subject-matter knowledge may be
insufficient to identify all important confounders or to rule out variables that
induce or amplify bias. Thus there is no guarantee that doubly robust machine
learning estimators will have a small bias.
Second, the implementation of doubly robust estimators has been difficult—
and computationally expensive when combined with machine learning—in high-
dimensional settings with time-varying treatments. This is especially true for
causal survival analysis. As a result, most published examples of causal infer-
ence from complex longitudinal data use single robust estimators, which are
the ones we have largely emphasized in Part III of this book. However, the
methods outlined in this chapter are quickly becoming routine in some fields.
Third, doubly robust machine learning can yield a variance of the causal
effect that equals the variance that would have been obtained if the true condi-
tional expectations b(X) and π(X) were known. However, there is no guarantee
that such variance will be small enough for meaningful causal inference.
18.5 Variable selection is a difficult problem 245
Suppose that we obtain a doubly robust machine learning estimate of the
causal effect, as described in the previous section, only to find out that its
(correct) variance is too big to be useful. This will happen, even when we have
estimated the propensity score and outcome regression with small product bias,
if some of the covariates in X are strongly associated with the treatment A.
Then the probability of treatment π(X) may be near 0 or near 1 for individuals
with a particular value of X. As a result, the effect estimate will have a
very large variance and thus a very wide (but often correct) 95% confidence
interval. Since we do not like very wide 95% confidence intervals, even if
they are correct, we may be tempted to throw out the variables in X that
are causing the “problem” and then repeat the data analysis. If we did that,This result raises a puzzling philo-
sophical question: If the confidence
interval is invalid when we use the
data to rule out, say, 5 variables
that make the variance too large,
then why should the confidence in-
terval be valid if we had happened
to receive a dataset that did not in-
clude those 5 variables? Given that
we always work with datasets in
which some potential confounders
are not recorded, how should we in-
terpret confidence intervals in any
observational analysis?
we would be fundamentally changing the game. Using the data to discard
covariates in X that are associated with treatment, but not so much with the
outcome, makes it no longer possible to guarantee that the 95% confidence
interval around the effect estimate is valid. The tension between including all
potential confounders to eliminate bias and excluding some variables to reduce
the variance is hard to resolve.
Given all of the above, developing a clear set of general guidelines for vari-
able selection may not be possible. In fact, so much methodological research is
ongoing around these issues that this chapter cannot possibly be prescriptive.
As discussed in Section 13.5, the best scientific advice for causal inference may
be to carry out multiple sensitivity analyses: implement several analytic meth-
ods and inspect the resulting effect estimates. If the various effect estimates
are compatible, we will be more confident in the results. If the various effect
estimates are not compatible, our job as researchers is to try to understand
why.
246 Variable selection and high-dimensional data
Part III
Causal infe rence for time-varying treatments
Chapter 19
TIME-VARYING TREATMENTS
So far this book has dealt with fixed treatments which do not vary over time. However, many causal questions
involve treatments that vary over time. For example, we may be interested in estimating the causal effects of
medical treatments, lifestyle habits, employment status, marital status, occupational exposures, etc. Because
these treatments may take different values for a single individual over time, we refer to them as time-varying
treatments.
Restricting our attention to time-fixed treatments during Parts I and II of this book helped us introduce basic
concepts and methods. It is now time to consider more realistic causal questions that involve the contrast of
hypothetical interventions that are played out over time. Part III extends the material in Parts I and II to
time-varying treatments. This chapter describes some key terminology and concepts for causal inference with
time-varying treatments. Though we have done our best to simplify those concepts (if you don’t believe us, check
out the causal inference literature), this is still one of the most technical chapters in the book. Unfortunately,
further simplification would result in too much loss of rigor. But if you made it this far, you are qualified to
understand this chapter.
19.1 The causal effect of time-varying treatments
Consider a time-fixed treatment variable A (1: treated, 0: untreated) at time
zero of follow-up and an outcome variable Y measured 60 months later. We
have previously defined the average causal effect of A on the outcome Y as the
contrast between the mean counterfactual outcome Y
a=1
under treatment and
the mean counterfactual outcome Y
a=0
under no treatment, that is, E
Y
a=1
−
E
Y
a=0
. Because treatment status is determined at a single time (time zero)
for everybody, the average causal effect does not need to make reference to
the time at which treatment occurs. In contrast, causal contrasts that involve
time-varying treatments need to incorporate time explicitly.
To see this, consider a time-varying dichotomous treatment A
k
that may
change at every month k of follow-up, where k = 0, 1, 2...K with K = 59.For simplicity, we will provisionally
assume that no individuals were lost
to follow-up or died during this pe-
riod, and we will also assume that
all variables were perfectly mea-
sured.
For example, in a 5-year follow-up study of individuals infected with the hu-
man immunodeficiency virus (HIV), A
k
takes value 1 if the individual receives
antiretroviral therapy in month k, and 0 otherwise. No individuals received
treatment before the start of the study at time 0, i.e., A
−1
= 0 for all individ-
uals.
We use an overbar to denote treatment history, i.e.,
¯
A
k
= (A
0
, A
1
, ...A
k
) is
the history of treatment from time 0 to time k. When we refer to the entire
treatment history through K, we often represent
¯
A
K
as
¯
A without a subscript.For compatibility with many pub-
lished papers, we use zero-based in-
dexing for time. That is, the first
time of possible treatment is k = 0
rather than k = 1.
In our HIV study, an individual who receives treatment continuously through-
out the follow-up has treatment history
¯
A = (A
0
= 1, A
1
= 1, ...A
59
= 1) =
(1, 1, ...1), or
¯
A =
¯
1. Analogously, an individual who never receives treat-
ment during the follow-up has treatment history
¯
A = (0, 0, ...0) =
¯
0. Most
individuals are treated during part of the follow-up only, and therefore have
intermediate treatment histories with some 1s and some 0s—which we cannot
250 Time-varying treatments
represent as compactly as
¯
1 and
¯
0.
Suppose Y measures health status—with higher values of Y indicating
better health—at the end of follow-up at time K + 1 = 60. We wouldTo keep things simple, our exam-
ple considers an outcome measured
at a fixed time. However, the con-
cepts discussed in this chapter also
apply to time-varying outcomes and
failure time outcomes (see Techni-
cal Point 21.8).
like to estimate the average causal effect of the time-varying treatment
¯
A on
the outcome Y . But we can no longer define the average causal effect of a
time-varying treatment as a contrast at a single time k, because the contrast
E
Y
a
k
=1
−E
Y
a
k
=0
quantifies the effect of treatment A
k
at a single time k,
not the effect of the time-varying treatment A
k
at all times k between 0 and
59.
Indeed we will have to define the average causal effect as a contrast between
the counterfactual mean outcomes under two treatment strategies that involveRemember that we use lower-case
to denote possible realizations of a
random variable: a
k
is a realization
of treatment A
k
.
treatment at all times between the start (k = 0) and the end (k = K) of
the follow-up. As a consequence, the average causal effect of a time-varying
treatment is not uniquely defined. In the next section, we describe many
possible definitions of average causal effect for a time-varying treatment.
19.2 Treatment strategies
A treatment strategy—also referred to as a plan, policy, protocol, or regime—
is a rule to assign treatment at each time k of follow-up. For example, twoA general counterfactual theory to
compare treatment strategies was
first articulated by Robins (1986,
1987, 1997a).
treatment strategies are “always treat” and “never treat” during the follow-
up. The strategy “always treat” is represented by ¯a = (1, 1, ...1) =
¯
1, and
the strategy “never treat” is represented by ¯a = (0, 0, ...0) =
¯
0. We can now
define an average causal effect of
¯
A on the outcome Y as the contrast between
the mean counterfactual outcome Y
¯a=
¯
1
under the strategy “always treat” and
the mean counterfactual outcome Y
¯a=
¯
0
under the strategy “never treat”, i.e.,
E
Y
¯a=
¯
1
− E
Y
¯a=
¯
0
.
But there are many other possible causal effects for the time-varying treat-
ment
¯
A, each of them defined by a contrast of outcomes under two particular
treatment strategies. For example, we might be interested in the average causal
effect defined by the contrast E [Y
¯a
]−E
h
Y
¯a
′
i
that compares the strategy “treat
at every other month” ¯a = (1, 0, 1, 0...) with the strategy “treat at all months
except the first one” ¯a
′
= (0, 1, 1, 1...). The number of possible contrasts is
very large: we can define at least 2
K
treatment strategies because there are 2
K
possible combinations of values (a
0
, a
1
, ...a
K
) for a dichotomous a
k
. In fact, as
we next explain, these 2
K
such strategies do not exhaust all possible treatment
strategies.
To define even more treatment strategies in our HIV example, consider the
time-varying covariate L
k
which denotes CD4 cell count (in cells/µL) measured
at month k in all individuals. The variable L
k
takes value 1 when the CD4 cell
count is low, which indicates a bad prognosis, and 0 otherwise. At time zero,
all individuals have a high CD4 cell count, L
0
= 0. We could then consider
the strategy “do not treat while L
k
= 0, start treatment when L
k
= 1 and
treat continuously after that time”. This treatment strategy is different from
the ones considered in the previous paragraph because we cannot represent it
by a rule ¯a = (a
0
, a
1
, ...a
K
) under which all individuals get the same treatment
a
0
at time k = 0, a
1
at time k = 1, etc. Now, at each time, some individuals
will be treated and others will be untreated, depending on the value of their
evolving L
k
. This is an example of a dynamic treatment strategy, a rule in
which the treatment a
k
at time k depends on the evolution of an individual’s
19.3 Sequentially randomized experiments 251
Fine Point 19.1
Deterministic and random treatment strategies. A deterministic dynamic treatment strategy is a rule g =
g
0
(¯a
−1
, l
0
) , ... g
K
¯a
K−1
,
¯
l
K
, where g
k
¯a
k−1
,
¯
l
k
specifies the treatment assigned at k to an individual with
past history
¯a
k−1
,
¯
l
k
. An example in our HIV study: g
k
¯a
k−1
,
¯
l
k
is 1 if an individual’s CD4 cell count (a func-
tion of
¯
l
k
) was low at or before k; otherwise g
k
¯a
k−1
,
¯
l
k
is 0. A deterministic static treatment strategy is a rule
g = [g
0
(¯a
−1
) , ... g
K
(¯a
K−1
)], where g
k
(¯a
k−1
) does not depend on
¯
l
k
. We will often abbreviate g
k
¯a
k−1
,
¯
l
k
as
g
¯a
k−1
,
¯
l
k
.
Most static and dynamic strategies we are interested in comparing are deterministic treatment strategies, which assign
a particular value of treatment (0 or 1) to each individual at each time. More generally, we could consider random
treatment strategies that do not assign a particular value of treatment, but rather a probability of receiving a treatment
value. Random treatment strategies can be static (e.g., “independently at each month, treat individuals with probability
0.3 and do not treat with probability 0.7”) or dynamic (e.g., “independently at each month, treat individuals whose
CD4 cell count is low with probability 0.3, but do not treat individuals with high CD4 cell count”).
We refer to the strategy g for which the mean counterfactual outcome E [Y
g
] is maximized (when higher values of
outcome are better) as the optimal treatment strategy. For a drug treatment, the optimal strategy will almost always
be dynamic because treatment needs to be discontinued when toxicity develops. Also, no random strategy can ever be
preferred to the optimal deterministic strategy. However, random strategies (i.e., randomized trials) remain scientifically
necessary because, before the trial, it is unknown which deterministic strategy is optimal. See Young et al. (2014) for
a taxonomy of treatment strategies. In the text, except if noted otherwise, the letter g will refer only to deterministic
treatment strategies.
time-varying covariate(s)
¯
L
k
. Strategies ¯a for which treatment does not depend
on covariates are non-dynamic or static treatment strategies. See Fine Point
19.1 for a formal definition.
Causal inference with time-varying treatments involves the contrast of coun-
terfactual outcomes under two or more treatment strategies. The average
causal effect of a time-varying treatment is only well-defined if the treatment
strategies of interest are specified. In our HIV example, we can define an
average causal effect based on the difference E [Y
¯a
] − E
h
Y
¯a
′
i
that contrasts
strategy ¯a (say, “always treat”) versus strategy ¯a
′
(say, “never treat”), or on
the difference E [Y
¯a
] −E [Y
g
] that contrasts strategy ¯a (“always treat”) versus
strategy g (say, “treat only after CD4 cell count is low”). Note we will often use
g to represent any—static or dynamic—strategy. When we use it to represent
a static strategy, we sometimes write Y
g=¯a
rather than just Y
g
or Y
¯a
.
That is, there is not a single definition of causal effect for time-varying
treatments. Even when only two treatment options—treat or do not treat—
exist at each time k, we can still define as many causal effects as pairs of
treatment strategies exist. In the next section, we describe a study design
under which all these causal effects can be validly estimated: the sequentially
randomized experiment.
19.3 Sequentially randomized experiments
The causal diagrams in Figures 19.1, 19.2, and 19.3 summarize three situations
that can occur in studies with time-varying treatments. In all three diagrams,
A
k
represents the time-varying treatment, L
k
the set of measured variables, Y
the outcome, and U
k
the set of unmeasured variables at k that are common
252 Time-varying treatments
Technical Point 19.1
On the definition of dynamic strategies. Each dynamic strategy g =
g
0
¯a
−1
,
¯
l
0
, ... g
K
¯a
K−1
,
¯
l
K
that depends
on past treatment and covariate history is associated with a dynamic strategy g
′
=
g
′
0
¯
l
0
, ... g
′
K
¯
l
K
that depends
only on past covariate history. By consistency (see Technical Point 19.2), an individual will have the same treatment,
covariate, and outcome history when following strategy g from time zero as when following strategy g
′
from time
zero. In particular, Y
g
= Y
g
′
and
¯
L
g
(K) =
¯
L
g
′
(K). Specifically, g
′
is defined in terms of g recursively by g
′
0
(l
0
) =
g
0
(¯a
−1
= 0, l
0
) (by convention, ¯a
−1
can only take the value zero) and g
′
k
¯
l
k
= g
k
g
′
k
¯
l
k−1
,
¯
l
k
. For any strategy
g for which treatment at each k already does not depend on past treatment history, g and g
′
are the identical set of
functions. The above definition of g
′
in terms of g guarantees that an individual has followed strategy g through time t
in the observed data, i.e., A
k
= g
k
¯
A
k−1
,
¯
L
k
for k ≤ t, if and only if the individual has followed strategy g
′
through
t, i.e., A
k
= g
′
k
¯
L
k
for k ≤ t.
causes of at least two other variables on the causal graph. Because the covari-By definition, a causal graph must
always include all common causes
of any two variables on the graph.
ates U
k
are not measured, their values are unknown and therefore unavailable
for the analysis. In our HIV study, the time-varying CD4 cell count L
k
is a
consequence of the true, but unmeasured, chronic damage to the immune sys-
tem U
k
. The greater an individual’s immune damage U
k
, the lower her CD4
Figure 19.1
cell count L
k
and her health status Y . For simplicity, the causal diagrams
show only the first two times of follow-up k = 0 and k = 1, and we assume
that all participants adhered to the assigned treatment.
The causal diagram in Figure 19.1 lacks arrows from either the measured
Figure 19.2
covariates
¯
L
k
or the unmeasured covariates
¯
U
k
into treatment A
k
. The causal
diagram in Figure 19.2 has arrows from the measured covariates
¯
L
k
, but not
from the unmeasured covariates
¯
U
k
, into treatment A
k
. The causal diagram
in Figure 19.3 has arrows from both the measured covariates
¯
L
k
and the un-
measured covariates
¯
U
k
into treatment A
k
.
Figure 19.3
Figure 19.1 could represent a randomized experiment in which treatment
A
k
at each time k is randomly assigned with a probability that depends only
on prior treatment history (for simplicity, we will assume perfect adherence
throughout). Our HIV study would be represented by Figure 19.1 if, e.g., an
individual’s treatment value at each month k were randomly assigned with
probability 0.5 for individuals who did not receive treatment during the previ-
ous month (A
k−1
= 0), and with probability 1 for individuals who did receive
treatment during the previous month k (A
k−1
= 1). When interested in the
contrast of static treatment strategies, Figure 19.1 is the proper generalization
of no confounding by measured or unmeasured variables for time-varying treat-
ments. Under this causal diagram, the counterfactual outcome mean E [Y
¯a
]
if everybody had followed the static treatment strategy ¯a is simply the mean
outcome E
Y |A = ¯a
among those who followed the strategy ¯a. (Interestingly,
the same is not true for dynamic strategies. The counterfactual mean E [Y
g
]
under a dynamic strategy g that depends on the variables L is only the mean
outcome among those who followed the strategy g if the probability of receiving
treatment A
k
= 1 is exactly 0.5 at all times k at which treatment A
k
depends
on L
k
. Otherwise, identifying E [Y
g
] requires the application of g-methods to
data on L, A, and Y under either Figure 19.1 or Figure 19.2.)
Figure 19.2 could represent a randomized experiment in which treatment
A
k
at each time k is randomly assigned by the investigators with a probability
that depends on prior treatment and measured covariate history. Our study
would be represented by Figure 19.2 if, e.g., an individual’s treatment value
19.4 Sequential exchangeability 253
at each month k were randomly assigned with probability 0.4 for untreated
individuals with high CD4 cell count (A
k−1
= 0, L
k
= 1), 0.8 for untreated
individuals with low CD4 cell count (A
k−1
= 0, L
k
= 0), and 0.5 for previously
treated individuals, regardless of their CD4 cell count (A
k−1
= 1). In Figure
19.2, there is confounding by measured, but not unmeasured, variables for the
time-varying treatment.
An experiment in which treatment is randomly assigned at each time k to
each individual is referred to as a sequentially randomized experiment. There-
fore Figures 19.1 and 19.2 could represent sequentially randomized experi-
ments. On the other hand, Figure 19.3 cannot represent a randomized experi-
ment: the value of treatment A
k
at each time k depends partly on unmeasured
variables U which are causes of L
k
and Y , but unmeasured variables obviously
cannot be used by investigators to assign treatment. That is, a sequentially
randomized experiment can be represented by a causal diagram with many
time points k = 0, 1...K and with no direct arrows from the unmeasured prog-
nostic factors U into treatment A
k
at any time k.
In observational studies, decisions about treatment often depend on out-
come predictors such as prognostic factors. Therefore, observational studies
will be typically represented by either Figure 19.2 or Figure 19.3 rather than
Figure 19.1. For example, suppose our HIV follow-up study were an observa-
tional study (not an experiment) in which the lower the CD4 cell count L
k
, the
more likely a patient is to be treated. Then our study would be represented by
Figure 19.2 if, at each month k, treatment decisions in the real world were made
based on the values of prior treatment and CD4 cell count history (
¯
A
k−1
,
¯
L
k
),
but not on the values of any unmeasured variables
¯
U
k
. Thus, an observational
study represented by Figure 19.2 would differ from a sequentially randomized
experiment only in that the assignment probabilities are unknown (but could
be estimated from the data). Unfortunately, it is impossible to show empiri-
cally whether an observational study is represented by the causal diagram in
either Figure 19.2 or Figure 19.3. Observational studies represented by Figure
19.3 have unmeasured confounding, as we describe later.
Sequentially randomized experiments are not frequently used in practice.
However, the concept of sequentially randomized experiment is helpful to un-
derstand some key conditions for valid estimation of causal effects of time-
varying treatments. The next section presents these conditions formally.
19.4 Sequential exchangeability
As described in Parts I and II, valid causal inferences about time-fixed treat-
ments typically require conditional exchangeability Y
a
⊥⊥A|L. When exchange-
ability Y
a
⊥⊥A|L holds, we can obtain unbiased estimates of the causal effect of
treatment A on the outcome Y if we appropriately adjust for the variables in L
via standardization, IP weighting, g-estimation, or other methods. We expect
conditional exchangeability to hold in conditionally randomized experiments—
a trial in which individuals are assigned treatment with a probability that de-
pends on the values of the covariates L. Conditional exchangeability holds in
observational studies if the probability of receiving treatment depends on the
measured covariates L and, conditional on L, does not further depend on any
unmeasured, common causes of treatment and outcome.
Similarly, causal inference with time-varying treatments requires adjusting
for the time-varying covariates
¯
L
k
to achieve conditional exchangeability at
254 Time-varying treatments
each time point, i.e., sequential conditional exchangeability. For example, in a
study with two time points, sequential conditional exchangeability is the com-
bination of conditional exchangeability at both the first time and the second
time of the study. That is, Y
g
⊥⊥A
0
|L
0
and Y
g
⊥⊥A
1
|A
0
= g(L
0
), L
0
, L
1
. (ForFor those with treatment history
[A
0
= g(L
0
), A
1
= g(A
0
, L
0
, L
1
)]
equal to (i.e., compatible with)
the treatment they would have
received under strategy g through
the end of follow-up, the coun-
terfactual outcome Y
g
is equal
(by consistency) to the observed
outcome Y and therefore also to
the counterfactual outcome under
the static strategy (a
0
, a
1
) with
a
0
= A
0
, a
1
= A
1
.
brevity, in this book we drop the word “conditional” and simply say sequen-
tial exchangeability.) We will refer to this set of conditional independences
as sequential exchangeability for Y
g
under any—static or dynamic—strategy g
that involves interventions on both components of the time-varying treatment
(A
0
, A
1
).
A sequentially randomized experiment—an experiment in which treatment
A
k
at each time k is randomly assigned with a probability that depends
only on the values of their prior covariate history
¯
L
k
and treatment history
¯
A
k−1
—implies sequential exchangeability for Y
g
. That is, for any strategy
g, the treated and the untreated at each time k are exchangeable for Y
g
conditional on prior covariate history
¯
L
k
and any observed treatment history
¯
A
k−1
= g(
¯
A
k−2
,
¯
L
k−1
) compatible with strategy g. Formally, sequential ex-
changeability for Y
g
is defined as
Y
g
⊥⊥A
k
|
¯
A
k−1
= g(
¯
A
k−2
,
¯
L
k−1
),
¯
L
k
for all strategies g and k = 0, 1...K
This form of sequential exchangeability (there are others, as we will see)In Figure 19.1, sequential uncondi-
tional exchangeability for Y holds,
i.e., for all static strategies ¯a,
Y
¯a
⊥⊥A
k
|
¯
A
k−1
= ¯a
k−1
. Un-
conditional exchangeability implies
that association is causation, i.e.,
E [Y
¯a
] = E
Y |
¯
A = ¯a
.
always holds in any causal graph which, like Figure 19.2, has no arrows from
the unmeasured variables U into the treatment variables A. Therefore sequen-
tial exchangeability for Y
g
holds in sequentially randomized experiments and
observational studies in which the probability of receiving treatment at each
time depends on their treatment and measured covariate history
¯
A
k−1
,
¯
L
k
and, conditional on this history, does not depend on any unmeasured causes
of the outcome.
That is, in observational studies represented by Figure 19.2 the mean of
the counterfactual outcome E [Y
g
] under all strategies g is identified, whereasWhenever we talk about identifica-
tion of causal effects, the identify-
ing formula will be the g-formula
(see Chapter 21). In rare cases not
relevant to our discussion, effects
can be identified by formulas that
are related to, but not equal to,
the g-formula (e.g., Technical Point
7.3).
in observational studies represented by Figure 19.3 no mean counterfactual
outcome E [Y
g
] is identified. In observational studies represented by other
causal diagrams, the mean counterfactual outcome E [Y
g
] under some but not
all strategies g is identified.
For example, consider an observational study represented by the causal di-
agram in Figure 19.4, which includes an unmeasured variable W
0
. In our HIV
example, W
0
could be an indicator for a scheduled clinic visit at time 0 that
was not recorded in our database. In that case W
0
would be a cause shared by
treatment A
0
and the measured (with some error) CD4 cell count L
1
, with U
1
representing the underlying but unknown true value of CD4 cell count. Even
Figure 19.4
though W
0
is unmeasured, the mean counterfactual outcome is still identified
under any static strategy g = ¯a; however, the mean counterfactual outcome
E [Y
g
] is not identified under any dynamic strategy g with treatment assign-
ment depending on L
1
. To illustrate why identification is possible under some
but not all strategies, we will use SWIGs in the next section.
In addition to some form of sequential exchangeability, causal inference
involving time-varying treatments also requires a sequential version of the con-
ditions of positivity and consistency. In a sequentially randomized experiment,
both sequential positivity and consistency are expected to hold (see Technical
Point 19.2). Below we will assume that sequential positivity and consistency
hold. Under the three identifiability conditions, we can identify the mean coun-
terfactual outcome E [Y
g
] under a strategy of interest g as long as we use meth-
ods that appropriately adjust for treatment and covariate history
¯
A
k−1
,
¯
L
k
,
such as the g-formula (standardization), IP weighting, and g-estimation.
19.5 Identifiability under some but not all treatment strategies 255
Technical Point 19.2
Positivity and consistency for time-varying treatments. The positivity condition needs to be generalized from the
fixed version “if f
L
(l) = 0, f
A|L
(a|l) > 0 for all a and l” to the sequential version
If f
¯
A
k−1
,
¯
L
k
¯a
k−1
,
¯
l
k
= 0, then f
A
k
|
¯
A
k−1
,
¯
L
k
a
k
|¯a
k−1
, l
k
> 0 for all
¯a
k
, l
k
In a sequentially randomized experiment, positivity will hold if the randomization probabilities at each time k are never
either 0 nor 1, no matter the past treatment and covariate history. If we are interested in a particular strategy g, the
above positivity condition needs to only hold for treatment histories compatible with g, i.e., for each k, a
k
= g
¯a
k−1
, l
k
.
The consistency condition also needs to be generalized from the fixed version “If A = a for a given individual, then
Y
a
= Y for that individual” to the sequential version
Y
¯a
= Y
¯a
∗
if a
∗
= a; Y
¯a
= Y if A = ¯a;
¯
L
¯a
k
=
¯
L
¯a
∗
k
if a
∗
k−1
= a
k−1
;
¯
L
¯a
k
=
¯
L
k
if A
k−1
= a
k−1
where
¯
L
¯a
k
is the counterfactual L-history through time k under strategy a. Technically, the identification of effects of
time-varying treatments on Y requires weaker consistency conditions: “If A = a for a given individual, then Y
¯a
= Y
for that individual” is sufficient for static strategies, and “For any strategy g, if A
k
= g
k
A
k−1
, L
k
at each time k for
a given individual, then Y
g
= Y ” is sufficient for dynamic strategies. However, the stronger sequential consistency is a
natural condition that we will always accept.
Note that, if we expect that the interventions “treat in month k” corresponding to A
k
= 1 and “do not treat in
month k” corresponding to A
k
= 0 are sufficiently well defined at all times k, then all static and dynamic strategies
involving A
k
will be similarly well defined.
19.5 Identifiability under some but not all treatment strategies
In Chapter 7, we presented a graphical rule—the backdoor criterion—to assessPearl and Robins (1995) proposed
a generalized backdoor criterion for
static strategies. Robins (1997a)
extended the procedure to dynamic
strategies.
whether exchangeability holds for a time-fixed treatment under a particular
causal diagram. The backdoor criterion can be generalized for time-varying
Figure 19.5
treatments. For example, for static strategies, a sufficient condition for iden-
tification of the causal effect of treatment strategies is that, at each time k,
all backdoor paths into A
k
that do not go through any future treatment are
blocked.
However, the generalized backdoor criterion does not directly show theconnection
Figure 19.6
between blocking backdoor paths and sequential exchangeability, because the
procedure is based on causal directed acyclic graphs that do not include coun-
terfactual outcomes. An alternative graphical check for identifiability of causal
effects is based on SWIGs, also discussed in Chapter 7. SWIGs are especially
helpful for time-varying treatments.
Consider the causal diagrams in Figures 19.5 and 19.6, which are simplified
versions of those in Figures 19.2 and 19.4. We have omitted the nodes U
0
and
L
0
and the arrow from A
0
to U
1
. In addition, the arrow from L
1
to Y is absent
so L
1
is no longer a direct cause of Y . Figures 19.5 and 19.6 (like Figures 19.2
and 19.4) differ in whether A
k
and subsequent covariates L
t
for t > k share a
cause W
k
.
As discussed in Part I of this book, a SWIG represents a counterfactual
world under a particular intervention. The SWIG in Figure 19.7 represents the
world in Figure 19.5 if all individuals had received the static strategy (a
0
, a
1
),
where a
0
and a
1
can take values 0 or 1. For example, Figure 19.7 can be used
to represent the world under the strategy “always treat” (a
0
= 1, a
1
= 1) or
under the strategy “never treat” (a
0
= 0, a
1
= 0). To construct this SWIG, we
256 Time-varying treatments
Technical Point 19.3
The many forms of sequential exchangeability. Consider a sequentially randomized experiment of a time-varying
treatment A
k
with multiple time points k = 0, 1, ...K. The SWIG that represents this experiment is just a longer version
of Figure 19.7. The following conditional independence can be directly read from the SWIG:
Y
a
, L
a
k+1
⊥⊥A
a
k−1
k
|
¯
A
a
k−2
k−1
,
¯
L
a
k−1
k
where L
a
k+1
is the counterfactual covariate history from time k + 1 through the end of follow-up. The above conditional
independence implies
Y
a
, L
a
k+1
⊥⊥A
a
k−1
k
|
¯
A
a
k−2
k−1
= a
k−1
,
¯
L
a
k−1
k
for the particular instance
¯
A
a
k−2
k−1
= a
k−1
, with a
k−1
being a component of strategy a. Because of consistency, the last conditional independence statement equals
Y
a
, L
a
k+1
⊥⊥A
k
|
¯
A
k−1
= a
k−1
,
¯
L
k
When this statement holds for all a, we say that there is sequential exchangeability . Interestingly, even though this
sequential exchangeability condition only refers to static strategies g = a, it is equivalent to the seemingly stronger
Y
g
, L
g
k+1
⊥⊥A
k
|
¯
A
k−1
= g
¯
A
k−1
,
¯
L
k
,
¯
L
k
for all g,
and, if positivity holds, is therefore sufficient to identify the outcome and covariate distribution under any static and dy-
namic strategies g (Robins 1986). This identification results from the joint conditional independence between
Y
a
, L
a
k+1
and A
k
. Note that, for dynamic strategies, sequential exchangeability does not follow from the separate independences
Y
a
⊥⊥A
k
|
¯
A
k−1
= a
k−1
,
¯
L
k
and L
a
k+1
⊥⊥A
k
|
¯
A
k−1
= a
k−1
,
¯
L
k
.
Stronger conditional independences are expected to hold in a sequentially randomized experiment, but they (i)
cannot be read from SWIGs and (ii) are not necessary for identification of the causal effects of treatment strate-
gies in the population. For example, a sequentially randomized trial implies the stronger joint independence
Y
a
, L
a
k+1
; all a
⊥⊥A
k
|
¯
A
k−1
,
¯
L
k
.
An even stronger condition that is expected to hold in sequentially randomized experiments is
Y
¯
A
,
¯
L
¯
A
⊥⊥A
k
|
¯
A
k−1
,
¯
L
k
where, for a dichotomous treatment A
k
,
¯
A denotes the set of all 2
K
static strategies ¯a, Y
¯
A
denotes the set of all
counterfactual outcomes Y
¯a
, and
¯
L
¯
A
denotes the set of all counterfactual covariate histories. Using a terminology
analogous to that of Technical Point 2.1, we refer to this joint independence condition as full sequential exchangeability.
first split the treatment nodes A
0
and A
1
. The right side of the split treat-
ments represents the value of treatment under the intervention. The left side
represents the value of treatment that would have been observed when inter-
vening on all previous treatments. Therefore, the left side of A
0
is precisely
Figure 19.7
A
0
because there are no previous treatments to intervene on, and the left side
of A
1
is the counterfactual treatment A
a
0
1
that would be observed after setting
A
0
to the value a
0
. All arrows into a given treatment in the original causal
diagram now point into the left side, and all arrows out of a given treatment
now originate from the right side. The outcome variable is the counterfac-
tual outcome Y
a
0
,a
1
and the covariates L are replaced by their corresponding
counterfactual variables. Note that we write the counterfactual variable cor-
responding to L
1
under strategy (a
0
, a
1
) as L
a
0
1
, rather than L
a
0
,a
1
1
, because a
future intervention on A
1
cannot affect the value of earlier L
1
.
Unlike the directed acyclic graph in Figure 19.5, the SWIG in Figure 19.7
does include the counterfactual outcome, which means that we can visually
check for exchangeability using d-separation.
19.5 Identifiability under some but not all treatment strategies 257
In Figure 19.7, by d-separation, both Y
a
0
,a
1
⊥⊥A
0
and Y
a
0
,a
1
⊥⊥A
a
0
1
|A
0
, L
a
0
1
hold for any static strategy (a
0
, a
1
). This second conditional independence
holds even though there seems to be an open path A
a
0
1
← a
0
→ L
a
0
1
← U
1
→
Y
a
0
,a
1
. However, this path is actually blocked for the following reason. In the
counterfactual world, a
0
is a constant and in probability statements constants
are always implicitly conditioned on even though, by convention, they are not
shown in the conditioning event. See Fine Point 19.2 for details.
The second conditional independence Y
a
0
,a
1
⊥⊥A
a
0
1
|A
0
, L
a
0
1
implies, by def-
inition, Y
a
0
,a
1
⊥⊥A
a
0
1
|A
0
= a
0
, L
a
0
1
in the subset of individuals who received
treatment A
0
= a
0
. Therefore, by consistency, we conclude that Y
a
0
,a
1
⊥⊥A
0
Y
a
0
,a
1
⊥⊥A
a
0
1
|A
0
= a
0
, L
a
0
1
equals
Y
a
0
,a
1
⊥⊥A
1
|A
0
= a
0
, L
1
because,
by consistency, L
a
0
1
= L
1
and
A
a
0
1
= A
1
when A
0
= a
0
.
and Y
a
0
,a
1
⊥⊥A
1
|A
0
= a
0
, L
1
hold under the causal diagram in Figure 19.5,
which corresponds to the SWIG in Figure 19.7 where we can actually check
for exchangeability. If there were multiple time points, we would say that
Y
¯a
⊥⊥A
k
|
¯
A
k−1
= ¯a
k−1
,
¯
L
k
for k = 0, 1...K
We refer to the above condition as static sequential exchangeability for Y
¯a
,
Figure 19.8
which is weaker than sequential exchangeability for Y
g
, because it only re-
quires conditional independence between counterfactual outcomes Y
¯a
indexed
by static strategies g = ¯a and treatment A
k
. Static sequential exchangeabil-
ity is sufficient to identify the mean counterfactual outcome under any static
strategy g = ¯a. See also Technical Point 19.3.
Static sequential exchangeability also holds under the causal diagram in
Figure 19.6, as can be checked by applying d-separation to its corresponding
SWIG in Figure 19.8. Thus, in an observational study represented by Fig-
ure 19.6, we can identify the mean counterfactual outcome under any static
strategy (a
0
, a
1
). Let us return to Figure 19.5. Let us now assume that the
Figure 19.9
arrow from L
1
to A
1
were missing. In that case, the arrow from L
a
0
1
to A
a
0
1
would also be missing from the SWIG in Figure 19.7. It would then follow by
d-separation that sequential unconditional exchangeability holds, and there-
fore that the mean counterfactual outcome under any static strategy could be
identified without data on L
1
. Now let us assume that, in Figure 19.5, there
was an arrow from U
1
to A
1
. Then the SWIG in Figure 19.7 would include
an arrow from U
1
to A
a
0
1
, and so no form of sequential exchangeability would
hold. The counterfactual mean would not be identified under any strategy.
Figure 19.10
We now discuss SWIGs under dynamic treatment strategies. Figure 19.9
represents the world of Figure 19.5 under a dynamic strategy g = [g
0
, g
1
(L
1
)] in
which treatment A
0
is assigned a fixed value g
0
(either 0 or 1), and treatment A
1
at time k = 1 is assigned a value g
1
(L
g
1
) that depends on the value of L
g
1
that
was observed after having assigned treatment value g
0
at time k = 0. For
example, g may be the strategy “do no treat at time 0, treat at time 1 only if
CD4 cell count is low, i.e., if L
g
1
= 1”. Under this strategy g
0
= 0 for every-
body, and g
1
(L
g
1
) = 1 when L
g
1
= 1 and g
1
(L
g
1
) = 0 when L
g
1
= 0. Therefore
the SWIG includes an arrow from L
g
1
to g
1
(L
g
1
). This arrow was not part of
the original causal graph; it exists only in the counterfactual world associated
with this dynamic strategy. We therefore draw this arrow differently from the
others, even though we need to treat it as any other arrow when evaluating
d-separation. The outcome in the SWIG is the counterfactual outcome Y
g
under the dynamic strategy g which uses L
1
to assign treatment A
1
.
By applying d-separation to the SWIG in Figure 19.9, we find that both
Y
g
⊥⊥A
0
and Y
g
⊥⊥A
g
1
|A
0
= g
0
, L
g
1
hold for any strategy g. That is, sequential
exchangeability for Y
g
holds, which means that we can identify the mean
counterfactual outcome under all strategies g (see also Fine Point 19.2). This
result, however, does not hold for the causal diagram in Figure 19.6.
258 Time-varying treatments
Fine Point 19.2
Arrows from intervention nodes in SWIGs When drawing SWIGs, we include arrows from the node a into future
variables even though, in a single intervention world, a is a constant and thus cannot affect other variables. One reason
we do this is that is a convenient device to keep track of the variables directly affected by A in the original DAG. A
second reason is described in Technical Point 21.10.
To illustrate why this is important, consider two causal diagrams: 1) the causal DAG in Figure 7.14 and 2) a causal
DAG equal to Figure 7.14 except that it also includes a direct arrow from A to Y . The SWIGs corresponding to these
two DAGs would be identical if we did not include arrows leaving from a. As a result, we could not use the SWIG to
infer that the causal effect of A on Y is identified in DAG 1 (using the front door formula) but not in DAG 2. Therefore,
when using d-separation on a SWIG, we need to remember that all paths that include any intervention node a are
blocked even if we do not explicitly condition on a in the notation.
The same logic applies for any intervention node under deterministic strategies. Suppose that we include a baseline
confounder L
0
in Figure 19.9 and we consider a deterministic dynamic strategy with g
0
replaced by g
0
(L
0
). Then, when
checking Y
g
⊥⊥A
g
1
|A
0
, L
0
, L
g
1
, we do not need to explicitly condition also on g
0
(L
0
) because g
0
(L
0
) becomes a constant
conditional on L
0
. However, we need to remember that, when conditioning on L
0
, paths through g
0
(L
0
) are blocked.
When we instantiate A
0
at g (L
0
) and use consistency, the statistical independence Y
g
⊥⊥A
g
1
|A
0
, L
0
, L
g
1
becomes the
exchangeability condition Y
g
⊥⊥A
1
|A
0
= g (L
0
) , L
0
, L
1
described above.
On the other hand, under a random strategy g that assigns a random treatment value A
+,g
0
to each individual from
a distribution that possibly depends on L
0
, we would explicitly include A
+,g
0
on the SWIG (replacing g
0
(L
0
)) and
also in the conditioning event when we check for d-separation, because A
+,g
0
is no longer perfectly determined by L
0
.
Richardson and Robins (2013) showed that a necessary condition for identifiability by the g-formula for such a random
strategy is that Y
g
⊥⊥A
g
1
|A
0
, A
+,g
0
, L
0
, L
g
1
holds. They also considered strategies that depend on the natural value of
treatment (Robins et al. 2004), i.e., strategies that assign treatment A
+,g
t
at time t based on A
g
t
, for which they
provided exchangeability conditions that license identification by the extended g-formula. Strategies that depend on the
natural value of treatment have recently been referred to as “modified treatment policies”(Diaz et al. 2021).
The SWIG in Figure 19.10 represents the world of Figure 19.6 under aWhat we read from the SWIG is
Y
g
⊥⊥A
g
1
|A
0
, L
g
1
which, by consis-
tency, implies Y
g
⊥⊥A
1
|A
0
= g
0
, L
1
dynamic treatment strategy g = [g
0
, g
1
(L
1
)]. By applying d-separation to the
Figure 19.11
Figure 19.12
SWIG in Figure 19.10, we find that Y
g
⊥⊥A
0
does not hold because of the open
path A
0
← W
0
→ L
g
1
→ g
1
(L
g
1
) → Y
g
. That is, sequential exchangeability for
Y
g
does not hold, which means that we cannot identify the mean counterfactual
outcome for any strategy g.
In summary, in observational studies (or sequentially randomized trials)
represented by Figure 19.5, sequential exchangeability for Y
g
holds, and there-
fore the data can be used to validly estimate causal effects involving static and
dynamic strategies. On the other hand, in observational studies represented by
Figure 19.6, only the weaker condition for static strategies holds, and therefore
the data can be used to validly estimate causal effects involving static strate-
gies, but not dynamic strategies. Another way to think about this is that in
the counterfactual world represented by the SWIG in Figure 19.10, the distri-
bution of Y
g
depends on the distribution of g
1
(L
g
1
) and thus of L
g
1
. However,
the distribution of L
g
1
is not identifiable due to the path A
0
← W
0
→ L
g
1
.
One last example. Consider Figure 19.11 which is equal to Figure 19.6
except for the presence of an arrow from L
1
to Y , and its corresponding SWIG
under a static strategy in Figure 19.12. We can use d-separation to show that
neither sequential exchangeability for Y
g
nor static sequential exchangeability
for Y
¯a
hold. Therefore, in observational study represented by Figure 19.11, we
cannot use the data to validly estimate causal effects involving any strategies.
19.6 Time-varying confounding and time-varying confounders 259
19.6 Time-varying confounding and time-varying confounders
No form of sequential exchangeability is guaranteed to hold in observational
studies. Achieving approximate exchangeability requires expert knowledge,
which will guide investigators in the design of their studies to measure as
many of the relevant variables
¯
L
k
as possible. For example, in an HIV study,
experts would agree that time-varying variables like CD4 cell count, viral load,
and symptoms need to be appropriately measured and adjusted for.
But the question “Are the measured covariates sufficient to ensure sequen-
tial exchangeability?” can never be answered with certainty. Yet we can use
our expert knowledge to organize our beliefs about exchangeability and rep-
resent them in a causal diagram. Figures 19.1 to 19.4 are examples of causal
diagrams that summarize different scenarios. Note that we drew these causal
diagrams in the absence of selection (e.g., censoring by loss to follow-up) so
that we can concentrate on confounding here.
Consider Figure 19.5. Like in Part I of this book, suppose that we are
interested in the effect of the time-fixed treatment A
1
on the outcome Y . We
say that there is confounding for the effect of A
1
on Y because A
1
and Y
share the cause U, i.e., because there is an open backdoor path between A
1
and Y through U. To estimate this effect without bias, we need to adjust for
confounders of the effect of the treatment A
1
on the outcome Y , as explained
in Chapter 7. In other words, we need to be able to block all open backdoor
paths between A
1
and Y . This backdoor path A
1
←− L
1
←− U −→ Y cannot
be blocked by conditioning on the common cause U because U is unmeasured
and therefore unavailable to the investigators. However, this backdoor path
can be blocked by conditioning on L
1
, which is measured. Thus, if the investi-
gators collected data on L
1
for all individuals, there would be no unmeasured
confounding for the effect of A
1
. We then say that L
1
is a confounder for
the effect of A
1
, even though the actual common cause of A
1
and Y was the
unmeasured U (re-read Section 7.3 if you need to refresh your memory about
confounding and causal diagrams).
As discussed in Chapter 7, the confounders do not have to be direct causesA second backdoor path gets open
after conditioning on collider L
1
:
A
1
←− A
0
−→ L
1
←− U −→ Y
This second backdoor path can be
safely blocked by conditioning on
prior treatment A
0
, assuming it is
available to investigators.
of the outcome. In Figure 19.5, the arrow from the confounder L
1
to the
outcome Y does not exist. Then the source of the confounding (i.e., the causal
confounder) is the unmeasured common cause U . Nonetheless, because data
on L
1
suffice to block the backdoor paths from A
1
to Y and thus to control
confounding, we refer to L
1
as a confounder for the effect of A
1
on Y .
Now imagine the very long causal diagram that contains all time points
k = 0, 1, 2..., and in which L
k
affects subsequent treatments A
k
, A
k+1
... and
shares unmeasured causes U
k
with the outcome Y . Suppose that we want to
estimate the causal effects on the outcome Y of treatment strategies defined
by interventions on A
0
, A
1
, A
2
. Then, at each time k, the covariate history
¯
L
k
will be needed, together with the treatment history
¯
A
k−1
, to block the back-
door paths between treatment A
k
and the outcome Y . Thus, no unmeasured
confounding for the effect of
¯
A requires that the investigators collected data
on
¯
L
k
for all individuals. We then say that the time-varying covariates in
¯
L
k
are time-varying confounders for the effect of the time-varying treatment
¯
A onTime-varying confounders are
sometimes referred to as time-
dependent confounders.
Y at several (or, in our example, all) times k in the study. See Fine Point 19.3
for a more precise definition of time-varying confounding.
Unfortunately, we cannot empirically confirm that all confounders, whether
time-fixed or time-varying, are measured. That is, we cannot empirically dif-
ferentiate between Figure 19.2 with no unmeasured confounding and Figure
19.3 with unmeasured confounding. Interestingly, even if all confounders were
260 Time-varying treatments
Fine Point 19.3
A definition of time-varying confounding. In the absence of selection bias, we say there is confounding for causal
effects involving E [Y
¯a
] if E [Y
¯a
] = E [Y |A = ¯a], that is, if the mean outcome had, contrary to fact, all individuals in
the study followed strategy ¯a differs from the mean outcome among the subset of individuals who followed strategy ¯a
in the actual study.
We say the confounding is solely time-fixed (i.e., wholly attributable to baseline covariates) if E [Y
¯a
|L
0
] =
E [Y |A = ¯a, L
0
], as would be the case if the only arrows pointing into A
1
in Figure 19.2 were from A
0
and L
0
. In
contrast, if the identifiability conditions hold, but E [Y
¯a
|L
0
] = E [Y |A = ¯a, L
0
], we say that time-varying confounding
is present. If the identifiability conditions do not hold, as in Figure 19.3, we say that there is unmeasured confounding.
A sufficient condition for no time-varying confounding is unconditional sequential exchangeability for Y
¯a
, i.e.,
Y
¯a
⊥⊥A
k
|
¯
A
k−1
= ¯a
k−1
. This condition holds in sequentially randomized experiments, like the one represented in
Figure 19.1, in which treatment A
k
at each time k is randomly assigned with a probability that depends only on the
values of prior treatment history
¯
A
k−1
. In fact, the causal diagram in Figure 19.1 can be greatly simplified. To do so,
first note that L
1
is not a common cause of any two nodes in the graph so it can be omitted from the graph. Once L
1
is gone, then both L
0
and U
1
can be omitted too because they cease to be common causes of two nodes in the graph.
In the graph without L
0
, L
1
, and U
1
, the node U
0
can be omitted too. That is, the causal diagram in Figure 19.1 can
be simplified to include only the nodes A
0
, A
1
and Y .
correctly measured and modeled, most adjustment methods may still result in
biased estimates when comparing treatment strategies. The next chapter ex-
plains why g-methods are the appropriate approach to adjust for time-varying
confounders.
Chapter 20
TREATMENT-CONFOUNDER FEEDBACK
The previous chapter identified sequential exchangeability as a key condition to identify the causal effects of time-
varying treatments. Suppose that we have a study in which the strongest form of sequential exchangeability holds:
the measured time-varying confounders are sufficient to validly estimate the causal effect of any treatment strategy.
Then the question is what confounding adjustment method to use. The answer to this question highlights a key
problem in causal inference about time-varying treatments: treatment-confounder feedback.
When treatment-confounder feedback exists, using traditional adjustment methods may introduce bias in the
effect estimates. That is, even if we had all the information required to validly estimate the average causal
effect of any treatment strategy, we would be generally unable to do so. This chapter describes the structure of
treatment-confounder feedback and the reasons why traditional adjustment methods fail.
20.1 The elements of treatment-confounder feedback
Consider again the sequentially randomized trial of individuals with HIV that
we discussed in the previous chapter. For every person in the study, we have
data on treatment A
k
(1: treated, 0: untreated) and covariates L
k
at each
month of follow-up k = 0, 1, 2...K, and on an outcome Y that measures health
status at month K + 1. The causal diagram in Figure 20.1, which is equal
Figure 20.1
to the one in Figure 19.2, represents the first two months of the study. The
time-varying covariates L
k
are time-varying confounders. (As in the previous
chapter, we are using this example without censoring so that we can focus on
confounding.)
Something else is going on in Figure 20.1. Not only is there an arrow from
CD4 cell count L
k
to treatment A
k
, but also there is an arrow from treatment
A
k−1
to future CD4 cell count L
k
—because receiving treatment A
k−1
increases
future CD4 cell count L
k
. That is, the confounder affects the treatment and
the treatment affects the confounder. There is treatment-confounder feedback
(see also Fine Point 20.1).
Figure 20.2
Note that time-varying confounding can occur without treatment-confounder
feedback. The causal diagram in Figure 20.2. is the same as the one in
Figure 20.1, except that the arrows from treatment A
k−1
to future L
k
and
U
k
have been deleted. In a setting represented by this diagram, the time-
varying covariates L
k
are time-varying confounders, but they are not affected
by prior treatment. Therefore, there is time-varying confounding, but there is
no treatment-confounder feedback.
Treatment-confounder feedback creates an interesting problem for causal
inference. To state the problem in its simplest form, let us simplify the causal
diagram in Figure 20.1 a bit more. Figure 20.3 is the smallest subset of Figure
20.1 that illustrates treatment-confounder feedback in a sequentially random-
ized trial with two time points. When drawing the causal diagram in Figure
20.3, we made four simplifications:
• Because our interest is in the implications of confounding by L
1
, we
262 Treatment-confounder feedback
Fine Point 20.1
Representing feedback cycles with acyclic graphs. Interestingly, an acyclic graph—like the one in Figure 20.1—can
be used to represent a treatment-confounder feedback loop or cycle. The trick to achieve this visual representation is
to elaborate the treatment-confounder feedback loop in time. That is, A
k−1
→ L
k
→ A
k
→ L
k+1
and so on.
The representation of feedback cycles with acyclic graphs also requires that time be considered as a discrete variable.
That is, we say that treatment and covariates can change during each interval [k, k + 1) for k = 0, 1, ...K, but we do
not specify when exactly during the interval the change takes place. This discretization of time is not a limitation in
practice: the length of the intervals can be chosen to be as short as the granularity of the data requires. For example,
in a study where individuals see their doctors once per month or less frequently (as in our HIV example), time may be
safely discretized into month intervals. In other cases, year intervals or day intervals may be more appropriate. Also, as
we said in Chapter 17, time is typically measured in discrete intervals (years, months, days) any way, so the discretization
of time is often not even a choice.
did not bother to include a node L
0
for baseline CD4 cell count. Just
suppose that treatment A
0
is marginally randomized and treatment A
1
is conditionally randomized given L
1
.
• The unmeasured variable U
0
is not included.
• There is no arrow from A
0
to A
1
, which implies that treatment is assigned
using information on L
1
only.
• There are no arrows from A
0
, L
1
and A
1
to Y , which would be the case
if treatment has no causal effect on the outcome Y of any individual, i.e.,
the sharp null hypothesis holds.
Figure 20.3
None of these simplifications affect the arguments below. A more compli-
cated causal diagram would not add any conceptual insights to the discussion
in this chapter; it would just be harder to read.
Now suppose that treatment has no effect on any individual’s Y , which im-
plies the causal diagram in Figure 20.3 is the correct one, but the investigators
do not know it. Also suppose that we have data on treatment A
0
in month 0
and A
1
in month 1, on the confounder CD4 cell count L
1
at the start of month 1,
and on the outcome Y at the end of follow-up. We wish to use these data to es-
timate the average causal effect of the static treatment strategy “always treat”,
(a
0
= 1, a
1
= 1), compared with the static treatment strategy “never treat”,
(a
0
= 0, a
1
= 0) on the outcome Y , i.e., E
Y
a
0
=1,a
1
=1
− E
Y
a
0
=0,a
1
=0
. Ac-
cording to Figure 20.3, the true, but unknown to the investigator, average
causal effect is 0 because there are no forward-directed paths from either treat-
ment variable to the outcome. That is, one cannot start at either A
0
or A
1
and, following the direction of the arrows, arrive at Y .
Figure 20.4
Figure 20.3 can depict a sequentially randomized trial because there are no
direct arrows from the unmeasured U into the treatment variables. Therefore,
as we discussed in the previous chapter, we should be able to use the observed
data on A
0
, L
1
, A
1
, and Y to conclude that E
Y
a
0
=1,a
1
=1
− E
Y
a
0
=0,a
1
=0
is equal to 0. However, as we explain in the next section, we will not generally
be able to correctly estimate the causal effect when we adjust for L
1
using tra-
ditional methods, like stratification, outcome regression, and matching. That
is, in this example, an attempt to adjust for the confounder L
1
using these
methods will generally result in an effect estimate that is different from 0, and
thus invalid.
20.2 The bias of traditional methods 263
In other words, when there are time-varying confounders and treatment-
confounder feedback, traditional methods cannot be used to correctly adjust
for those confounders. Even if we had sufficient longitudinal data to ensureFigure 20.3 represents either a se-
quentially randomized trial or an
observational study with no unmea-
sured confounding; Figure 20.4 rep-
resents an observational study.
sequential exchangeability, traditional methods would not generally provide a
valid estimate of the causal effect of any treatment strategies. In contrast,
g-methods appropriately adjust for the time-varying confounders even in the
presence of treatment-confounder feedback.
This limitation of traditional methods applies to settings in which the time-
varying confounders are affected by prior treatment as in Figure 20.3, but also
to settings in which the time-varying confounders share causes W with prior
treatment as in Figure 20.4, which is a subset of Figure 19.4. We refer to both
Figures 20.3 and 20.4 (and Figures 19.2 and 19.4) as examples of treatment-
confounder feedback. The next section explains why traditional methods can-
not adequately handle treatment-confounder feedback.
20.2 The bias of traditional methods
To illustrate the bias of traditional methods, let us consider a (hypothetical)
sequentially randomized trial with 32, 000 individuals with HIV and two timeThis is an ideal trial with full ad-
herence to the assigned treatment
strategy and no losses to follow-up.
points k = 0 and k = 1. Treatment A
0
= 1 is randomly assigned at baseline
with probability 0.5. Treatment A
1
is randomly assigned in month 1 with a
probability that depends only on the value of CD4 cell count L
1
at the start
of month 1—0.4 if L
1
= 0 (high), 0.8 if L
1
= 1 (low). The outcome Y ,
Table 20.1
N A
0
L
1
A
1
Mean Y
2400 0 0 0 84
1600 0 0 1 84
2400 0 1 0 52
9600 0 1 1 52
4800 1 0 0 76
3200 1 0 1 76
1600 1 1 0 44
6400 1 1 1 44
which is measured at the end of follow-up, is a function of CD4 cell count,
concentration of virus in the serum, and other clinical measures, with higher
values of Y signifying better health.
Table 20.1 shows the data from this trial. To save space, the table displays
one row per combination of values of A
0
, L
1
, and A
1
, rather than one row per
individual. For each of the eight combinations, the table provides the number
of subjects N and the mean value of the outcome E [Y |A
0
, L
1
, A
1
]. Thus, row 1
shows that the mean of the 2400 individuals with (A
0
= 0, L
1
= 0, A
1
= 0) was
E [Y |A
0
= 0, L
1
= 0, A
1
= 0] = 84. In this sequentially randomized trial, the
identifiability conditions—sequential exchangeability, positivity, consistency—
hold. By design, there are no confounders for the effect of A
0
on Y , and L
1
is
the only confounder for the effect of A
1
on Y so (conditional on L
1
) sequential
exchangeability holds. By inspection of Table 20.1, we can conclude that theIf there were additional times k at
which treatment A
k
were affected
by L
k
, then L
k
would be a time-
varying confounder
positivity condition is satisfied, because otherwise one or more of the eight
rows would have zero individuals.
The causal diagram in Figure 20.3 depicts this sequentially randomized ex-
periment when the sharp null hypothesis holds. To check whether the data in
Table 20.1 are consistent with the causal diagram in Figure 20.3, we can sepa-Figure 20.3 represents the null be-
cause there is no arrow from L
1
to
Y . Otherwise, A
0
would have an
effect on Y through L
1
rately estimate the average causal effects of each of the time-fixed treatments
A
0
and A
1
within levels of past covariates and treatment, which should all be
null. In the calculations below, we will ignore random variability.
A quick inspection of the table shows that the average causal effect of
treatment A
1
is indeed zero in all four strata defined by A
0
and L
1
. Consider
the effect of A
1
in the 4000 individuals with A
0
= 0 and L
1
= 0, whose data
are shown in rows 1 and 2 of Table 20.1. The mean outcome among those
who did not receive treatment at time 1, E [Y |A
0
= 0, L
1
= 0, A
1
= 0], is 84,
and the mean outcome among those who did receive treatment at time 1,
264 Treatment-confounder feedback
Technical Point 20.1
G-null test. Suppose the sharp null hypothesis is true. Then any counterfactual outcome Y
g
is the observed outcome
Y . In this setting, sequential exchangeability for all Y
g
can be written as Y ⊥⊥A
0
|L
0
and Y ⊥⊥A
1
|A
0
, L
0
, L
1
in a study
with two time points. (We have used the fact that, for any values of a
0
and l
0
, there exist strategies g such that
a
0
= g(l
0
).) Therefore, under sequential exchangeability, a test of these conditional independencies is a test of the
sharp null. This is the g-null test (Robins 1986). Note the first independence implies no causal effect of A
0
in any
strata defined by L
0
, and the second independence implies no causal effect of A
1
in any strata defined by L
1
and A
0
.
More generally, the g-null theorem of Robins (1986) says that, under sequential randomization for all g, the above
two independencies hold if and only if the distribution of Y
g
and therefore the mean E [Y
g
] is the same for all g, and
also equal to the distribution and mean of the observed Y .
E [Y |A
0
= 0, L
1
= 0, A
1
= 1], is also 84. Therefore the difference
E [Y |A
0
= 0, L
1
= 0, A
1
= 1] − E [Y |A
0
= 0, L
1
= 0, A
1
= 0]
is zero. Because the identifiability conditions hold, this associational difference
validly estimates the average causal effect
E
Y
a
1
=1
|A
0
= 0, L
1
= 0
− E
Y
a
1
=0
|A
0
= 0, L
1
= 0
in the stratum (A
0
= 0, L
1
= 0). Similarly, it is easy to check that the aver-
age causal effect of treatment A
1
on Y is zero in the remaining three strata
(A
0
= 0, L
1
= 1), (A
0
= 1, L
1
= 0), (A
0
= 1, L
1
= 1), by comparing the mean
outcome between rows 3 and 4, rows 5 and 6, and rows 7 and 8, respectively.
We can now show that the average causal effect of A
0
is also zero. To do so,
we need to compute the associational difference E [Y |A
0
= 1] − E [Y |A
0
= 0]
which, because of randomization, is a valid estimator of the causal contrast
E
Y
a
0
=1
− E
Y
a
0
=0
. The mean outcome E [Y |A
0
= 0] among the 16, 000
individuals treated at time 0 is the weighted average of the mean outcomes inThe weighted average is
2400
16000
× 84 +
1600
16000
× 84 +
2400
16000
× 52 +
9600
16000
× 52 = 60
rows 1, 2, 3 and 4, which is 60. And E [Y |A
0
= 1], computed analogously, is
also 60. Therefore, the average causal effect of A
0
is zero.
We have confirmed that the causal effects of A
0
and A
1
(conditional on
the past) are zero when we treat A
0
and A
1
separately as time-fixed treat-
ments. What if we now treat the joint treatment (A
0
, A
1
) as a time-varying
treatment and compare two treatment strategies? For example, let us say that
we want to compare the strategies “always treat” versus “never treat”, that is
(a
0
= 1, a
1
= 1) versus (a
0
= 0, a
1
= 0). Because the identifiability conditions
hold, the data in Table 20.1 should suffice to validly estimate this effect.
Because the effect for each of the individuals components of the strategy,
a
0
and a
1
, is zero, it follows from the g-null theorem (see Technical Point 20.1)
that the average causal effect E
Y
a
0
=1,a
1
=1
− E
Y
a
0
=0,a
1
=0
is zero. But is
this what we conclude from the data if we use conventional analytic methods?
To answer this question, let us conduct two data analyses. In the first one,
we do not adjust for the confounder L
1
, which should give us an incorrect
effect estimate. In the second one, we do adjust for the confounder L
1
via
stratification.
1. We compare the mean outcome in the 9600 individuals who were treated
at both times (rows 6 and 8 of Table 20.1) with that in the 4800 individ-
uals who were untreated at both times (rows 1 and 3). The respective
averages are E [Y |A
0
= 1, A
1
= 1] = 54.7, and E [Y |A
0
= 0, A
1
= 0] =
20.3 Why traditional methods fail 265
68. The associational difference is 54.7−68 = −13.3 which, if interpretedE [Y |A
0
= 1, A
1
= 1]
3200
9600
× 76 +
6400
9600
× 44 = 54.7
E [Y |A
0
= 0, A
1
= 0]
2400
4800
× 84 +
2400
4800
× 52 = 68.0
causally, would mean that not being treated at either time is better than
being treated at both times. This analysis gives the wrong answer—a
non-null difference—because E [Y |A
0
= a
0
, A
1
= a
1
] is not a valid esti-
mator of E [Y
a
0
,a
1
]. Adjustment for the confounder L
1
is needed.
2. We adjust for L
1
via stratification. That is, we compare the mean
outcome in individuals who were treated with that in individuals who
were untreated at both times, within levels of L
1
. For example, take
the stratum L
1
= 0. The mean outcome in the treated at both times,
E [Y |A
0
= 1, L
1
= 0, A
1
= 1], is 76 (row 6). The mean outcome in the un-
treated at both times, E [Y |A
0
= 0, L
1
= 0, A
1
= 0], is 84 (row 1). The
associational difference is 76 − 84 = −8 which, if interpreted causally,
would mean that, in the stratum L
1
= 0, not being treated at either
time is better than being treated at both times. Similarly, the differ-
ence E [Y |A
0
= 1, L
1
= 1, A
1
= 1] − E [Y |A
0
= 0, L
1
= 1, A
1
= 0] in the
stratum L
1
= 1 is also −8.Note that, because the effect is
−8 in both strata of L
1
, it is not
possible that a weighted average
of the stratum-specific effects will
yield the correct value 0.
What? We said that the effect estimate should be 0, not −8. How is
it possible that the analysis adjusted for the confounder also gives a wrong
answer? This estimate reflects the bias of traditional methods to adjust for
confounding when there is treatment-confounder feedback. The next section
explains why the bias arises.
20.3 Why traditional methods fail
Table 20.1 shows data from a sequentially randomized trial with treatment-
confounder feedback, as represented by the causal diagram in Figure 20.3. Even
though no data on the unmeasured variable U
1
(immunosuppression level) is
available, all three identifiability conditions hold: U
1
is not needed if we have
data on the confounder L
1
. Therefore, as discussed in Chapter 19, we should
be able to correctly estimate causal effects involving any static or dynamic
treatment strategies. And yet our analyses in the previous section did not
yield the correct answer, whether or not we adjusted for L
1
.
The problem was that we did not use the correct method to adjust for con-
founding. Stratification is a commonly used method to adjust for confounding,
but it cannot handle treatment-confounder feedback. Stratification means esti-
mating the association between treatment and outcome in subsets—strata—of
the study population defined by the confounders—L
1
in our example. Because
the variable L
1
can take only two values—1 if the CD4 cell count is low, and
0 otherwise—there are two such strata in our example. To estimate the causal
effect in those with L
1
= l, we selected (i.e., conditioned or stratified on) the
subset of the population with value L
1
= l.
Figure 20.5
But stratification can have unintended effects when the association measure
is computed within levels of a variable L
1
that is caused by prior treatment A
0
.
Indeed Figure 20.5 shows that conditioning on L
1
—a collider—opens the path
A
0
−→ L
1
←− U
1
−→ Y . That is, stratification induces a noncausal associa-
tion between the treatment A
0
at time 0 and the unmeasured variable U
1
, and
therefore between A
0
and the outcome Y , within levels of L
1
. Among those
with low CD4 count (L
1
= 1), being on treatment (A
0
= 1) becomes a marker
for severe immunosuppression (high value of U
1
); among those with a high level
266 Treatment-confounder feedback
Fine Point 20.2
Confounders on the causal pathway. Conditioning on confounders L
1
which are affected by previous treatment can
create selection bias even if the confounder is not on a causal pathway between treatment and outcome. In fact, no
such causal pathway exists in Figures 20.5 and 20.6.
On the other hand, in Figure 20.7 the confounder L
1
for subsequent treatment A
1
lies on a causal pathway from
earlier treatment A
0
to outcome Y , i.e., the path A
0
−→ L
1
−→ Y . If U
1
were not a common cause of L
1
and Y
in Figure 20.7 (i.e., if there were no selection bias), the A-Y associations within strata of L
1
would be an unbiased
estimate of the direct effects of A
0
on Y not through L
1
, but still would not be an unbiased estimate of the overall
effect of
¯
A on Y , because the effect of A
0
mediated through L
1
is not included.
It is sometimes said that variables on a causal pathway between treatment and outcome cannot be considered as
confounders, because adjusting for those variables will result in a biased effect estimate. However, this characterization
of confounders is inaccurate for time-varying treatments. Figure 20.7 shows that a confounder for subsequent treatment
A
1
can be on a causal pathway between past treatment A
0
and the outcome. As for whether adjustment for confounders
on a causal pathway induces bias for the effect of a treatment strategy, that depends on the choice of adjustment method.
Stratification will indeed induce bias; g-methods will not.
of CD4 (L
1
= 0), being off treatment (A
0
= 0) becomes a marker for milder
immunosuppression (low value of U
1
). Thus, the side effect of stratification is
to induce an association between treatment A
0
and outcome Y .
Figure 20.6
In other words, stratification eliminates confounding for A
1
at the cost of
introducing selection bias for A
0
. The associational differences
E [Y |A
0
= 1, L
1
= l, A
1
= 1] − E [Y |A
0
= 0, L
1
= l, A
1
= 0]
may be different from 0 even if, as in our example, treatment has no effect on
the outcome of any individuals at any time. This bias arises from choosing
a subset of the study population by selecting on a variable L
1
affected by (a
Figure 20.7
component A
0
of) the time-varying treatment. The net bias depends on the
relative magnitude of the confounding that is eliminated and the selection bias
that is created.
Technically speaking, the bias of traditional methods will occur not only
when the confounders are affected by prior treatment (in randomized experi-
ments or observational studies), but also when the confounders share an un-
measured cause W
0
with prior treatment (in observational studies). In the
observational study depicted in Figure 20.6, conditioning on the collider L
1
opens the path A
0
←− W
0
−→ L
1
←− U
1
−→ Y . For this reason, we referred
to both settings in Figures 20.3 and 20.4—which cannot be distinguished using
the observed data—as examples of treatment-confounder feedback.
The causal diagrams that we have considered to describe the bias of tra-
ditional methods are all very simple. They only represent settings in which
treatment does not have a causal effect on the outcome. However, conditioning
on a confounder in the presence of treatment-confounder feedback also induces
bias when treatment has a non-null effect, as in Figure 20.7. The presence of
arrows from A
0
, A
1
, or L
1
to Y does not change the fact that conditioning
on L
1
creates an association between A
0
and Y that does not have a causal
interpretation (see also Fine Point 20.2). Also, our causal diagrams had only
two time points and a limited number of nodes, but the bias of traditional
methods will also arise from high-dimensional data with multiple time points
and variables. In fact, the presence of time-varying confounders affected by
previous treatment at multiple times increases the possibility of a large bias.
20.4 Why traditional methods cannot be fixed 267
In general, valid estimation of the effect of treatment strategies is only
possible when the joint effect of the treatment components A
k
can be estimated
simultaneously and without bias. As we have just seen, this may be impossible
to achieve using stratification, even when data on all time-varying confounders
are available.
20.4 Why traditional methods cannot be fixed
We showed that stratification cannot be used as a confounding adjustment
method when there is treatment-confounder feedback. But what about other
traditional methods? For example, we could have used parametric outcome
regression, rather than nonparametric stratification, to adjust for confounding.
Would outcome regression succeed where plain stratification failed?
This question is particularly important for settings with high-dimensional
data, because in high-dimensional settings we will be unable to conduct a
simple stratified analysis like we did in the previous section. Consider data
generated under Figure 20.5. Treatment A
k
occurs at two months k = 0, 1,
which means that there are only 2
2
= 4 static treatment strategies ¯a. But
when the treatment A
k
occurs at multiple points k = 0, 1...K, we will not be
able to present a table with all the combinations of treatment values. If, as isThe number of data combinations
is even greater because there are
multiple confounders L
k
measured
at each time point k.
not infrequent in practice, K is of the order of 100, then there are 2
100
static
treatment strategies ¯a, a staggering number that far exceeds the sample size
of any study. The total number of treatment strategies is much greater when
we consider dynamic strategies as well.
As we have been arguing since Chapter 11, we will need modeling to es-
timate average causal effects involving E [Y
¯a
] when there are many possible
treatment strategies ¯a. To do so, we will need to hypothesize a dose-response
function for the effect of treatment history ¯a on the mean outcome Y . One
possibility would be to assume that the effect of treatment strategies ¯a in-
creases linearly as a function of the cumulative treatment under each strategy.
Under this assumption, all strategies that assign treatment for exactly three
months have the same effect, regardless of the period when those three months
of treatment occur the first 3 months of follow-up, the last 3 months of follow-
up, etc. The price paid for modeling is yet another threat to the validity of our
estimates due to possible model misspecification of the dose-response function.
And yet paying this price does not buy any protection against the failure of
traditional methods. In the presence of treatment-confounder feedback, regres-
sion modeling cannot possibly remove the bias of conventional stratification-
based methods because regression is a conventional stratification-based method
itself. For example, suppose that we have data generated under Figure 20.5.
Let us define cumulative treatment cum
¯
A
= A
0
+ A
1
, which can take 3
values: 0 (if the individuals remains untreated at both times), 1 (if the subject
is treated at time 1 only or at time 2 only), and 2 (if the subject is treated
at both times). The treatment strategies of interest can then be expressed
as “always treat” cum (¯a) = 2, and “never treat” cum (¯a) = 0, and the aver-
age causal effect as E
Y
cum(¯a)=2
− E
Y
cum(¯a)=0
. Again, any valid method
should estimate that the value of this difference is 0.
Under the assumption that the mean outcome E
Y |
¯
A, L
1
depends linearly
on the covariate cum
¯
A
, we could fit the outcome regression model
E
Y |
¯
A, L
1
= θ
0
+ θ
1
cum
¯
A
+ θ
2
L
1
268 Treatment-confounder feedback
The associational difference E
Y |cum
¯
A
= 2, L
1
−E
Y |cum
¯
A
= 0, L
1
is
equal to θ
1
×2. (The model correctly assumes that the difference is the same in
the strata L
1
= 1 and L
1
= 0.) Therefore some might want to interpret θ
1
×2
as the average causal effect of “always treat” versus “never treat” within levels
of the covariate L
1
. But such causal interpretation is unwarranted because, as
Figure 20.5 shows, conditioning on L
1
induces an association between A
0
, a
component of treatment cum
¯
A
, and the outcome Y . This implies that θ
1
—
and therefore the associational difference of means—is non-zero even if the
true causal effect is zero and the regression model for E
Y |
¯
A, L
1
is correct.
A similar argument can be applied to matching. G-methods are needed to
appropriately adjust for time-varying confounders in the presence of treatment-
confounder feedback.
20.5 Adjusting for past treatment
One more thing before we discuss g-methods. For simplicity, we have so far
Figure 20.8
Figure 20.9
Figure 20.10
described treatment-confounder feedback under simplified causal diagrams in
which past treatment does not directly affect subsequent treatment. That is,
the causal diagrams in Figures 20.3 and 20.4 did not include an arrow from A
0
to A
1
. We now consider the more general case in which past treatment may
directly affect subsequent treatment.
As an example, suppose doctors in our HIV study use information on past
treatment history
¯
A
k−1
when making a decision about whether to prescribe
treatment A
k
at time k. To represent this situation, we add an arrow from A
0
to A
1
to the causal diagrams in Figures 20.3 and 20.4, as depicted in Figures
20.8 and 20.9.
The causal diagrams in Figures 20.8 and 20.9 show that, in the presence of
treatment-confounder feedback, conditioning on L
1
is insufficient to block all
backdoor paths between treatment A
1
and outcome Y . Indeed conditioning
on L
1
opens the path A
1
← A
0
→ L
1
← U
1
→ Y in Figure 20.8, and the
path A
1
← A
0
← W
0
→ L
1
← U
1
→ Y in Figure 20.9. Of course, regardless
of whether treatment-confounder feedback exists, conditioning on past treat-
ment history is always required when past treatment has a non-null effect on
the outcome, as in the causal diagram of Figure 20.10. Under this diagram,
treatment A
0
is a confounder of the effect of treatment A
1
.
Therefore, sequential exchangeability at time k generally requires condition-
ing on treatment history
¯
A
k−1
before k; conditioning only on the covariates L
is not enough. That is why, in this and in the previous chapter, all the con-
ditional independence statements representing sequential exchangeability were
conditional on treatment history.
Past treatment plays an important role in the estimation of effects of time-
fixed treatments too. Suppose we are interested in estimating the effect of
the time-fixed treatment A
1
—as opposed to the effect of a treatment strat-
egy involving both A
0
and A
1
—on Y . (Sometimes the effect of A
1
is re-
ferred to as the short-term effect of the time-varying treatment
¯
A.) Then
lack of adjustment for past treatment A
0
will generally result in selection
bias if there is treatment-confounder feedback, and in confounding if past
treatment A
0
directly affects the outcome Y . In other words, the difference
E [Y |A
1
= 1, L
1
]−E [Y |A
1
= 0, L
1
] would not be zero even if treatment A
1
had
no effect on any individual’s outcome Y , as in Figures 20.8-20.10. In practice,
when making causal inferences about time-fixed treatments, bias may arise in
20.5 Adjusting for past treatment 269
analyses that compare current users (A
1
= 1) versus nonusers (A
1
= 0) of
treatment. To avoid the bias, one can adjust for prior treatment history or
restrict the analysis to individuals with a particular treatment history. This
is the idea behind “new-user designs” for time-fixed treatments: restrict theIf one could correctly adjust for past
treatment, the analysis would not
need to be restricted to new users.
analysis to individuals who had not used treatment in the past.
The requirement to adjust for past treatment has additional bias impli-
cations when past treatment is mismeasured. As discussed in Section 9.3,
a mismeasured confounder may result in effect estimates that are biased, ei-
ther upwards or downwards. In our HIV example, suppose investigators did
not have access to the study participants’ medical records. Rather, to ascer-
tain prior treatment, investigators had to ask participants via a questionnaire.
Since not all participants provided an accurate recollection of their treatment
history, treatment A
0
was measured with error. Investigators had data on
the mismeasured variable A
∗
0
rather than on the variable A
0
. To depict this
setting in Figures 20.8-20.10, we add an arrow from the true treatment A
0
to
the mismeasured treatment A
∗
0
, which shows that conditioning on A
∗
0
cannot
block the biasing paths between A
1
and Y that go through A
0
. Investigators
will then conclude that there is an association between A
1
to Y , even after
adjusting for A
∗
0
and L
1
, despite the lack of an effect of A
1
on Y .
Therefore, when treatment is time-varying, we find that, contrary to a
widespread belief, mismeasurement of treatment—even if the measurement er-
ror is independent and non-differential—may cause bias under the null. ThisRobins (1987) showed that ran-
domly mismeasured treatment may
lead to bias away from the null.
bias arises because past treatment is a confounder for the effect of subsequent
treatment, even if past treatment has no causal effect on the outcome. Fur-
thermore, under the alternative, this imperfect bias adjustment may result in
an exaggerated estimate of the effect.
270 Treatment-confounder feedback
Chapter 21
G-METHODS FOR TIME-VARYING TREATMENTS
In the previous chapter we described a dataset with a time-varying treatment and treatment-confounder feedback.
We showed that, when applied to this dataset, traditional methods for confounding adjustment could not correctly
adjust for confounding. Even though the time-varying treatment had a zero causal effect on the outcome, traditional
adjustment methods yielded effect estimates that were different from the null.
This chapter describes the solution to the bias of traditional methods in the presence of treatment-confounder
feedback: the use of g-methods—the g-formula, IP weighting, g-estimation, and their doubly-robust generalizations.
Using the same dataset as in the previous chapter, here we show that the three g-methods yield the correct (null)
effect estimate. For time-fixed treatments, we described the g-formula in Chapter 13, IP weighting of marginal
structural models in Chapter 12, and g-estimation of structural nested models in Chapter 15. Here we introduce
each of the three g-methods for the comparison of static treatment strategies under the identifiability conditions
described in Chapter 19: sequential exchangeability, positivity, and consistency.
21.1 The g-formula for time-varying treatments
Consider again the data from the sequentially randomized experiment in Table
20.1 which, for convenience, we reproduce again here as Table 21.1. Suppose
Table 21.1
N A
0
L
1
A
1
Mean Y
2400 0 0 0 84
1600 0 0 1 84
2400 0 1 0 52
9600 0 1 1 52
4800 1 0 0 76
3200 1 0 1 76
1600 1 1 0 44
6400 1 1 1 44
we are only interested in the effect of the time-fixed treatment A
1
. That is,
suppose we want to contrast the mean counterfactual outcomes E
Y
a
1
=1
and
E
Y
a
1
=0
. In Parts I and II we have showed that, under the identifiabil-
ity conditions, each of the means E [Y
a
1
] is a weighted average of the mean
outcome E [Y |A
1
= a
1
, L
1
= l
1
] conditional on the (time-fixed) treatment and
confounders. Specifically, E [Y
a
1
] equals the weighted average
X
l
1
E [Y |A
1
= a
1
, L
1
= l
1
] f (l
1
) , where f (l
1
) = Pr [L
1
= l
1
] .
because, as shown in the previous chapter, only L
1
is needed to make the
treated (A
1
= 1) and the untreated (A
1
= 0) conditionally exchangeable. This
weighted average is the g-formula for E [Y
a
1
]: the mean outcome standardized
to the distribution of the confounders (here, L
1
only) in the study population.
But, in the sequentially randomized experiment of Table 21.1, the treat-
ment A = (A
0
, A
1
) is time-varying and, as we saw in the previous chapter,
there is treatment-confounder feedback. That means that traditional adjust-
ment methods cannot be relied on to unbiasedly estimate the causal effect of
time-varying treatment A. For example, traditional methods may not provide
valid estimates of the mean outcome under “always treat” E
Y
a
0
=1,a
1
=1
and
the mean outcome under “never treat” E
Y
a
0
=0,a
1
=0
even in a sequentially
randomized experiment in which sequential exchangeability holds. In contrast,
the g-formula can be used to calculate the counterfactual means E [Y
a
0
,a
1
] in
a sequentially randomized experiment. To do so, the above expression of the
g-formula for time-fixed treatments needs to be generalized.
272 G-methods for time-varying treatments
The g-formula for E [Y
a
0
,a
1
] under the identifiability conditions (described
in Chapter 19) will still be a weighted average, but now it will be a weighted
average of the mean outcome E [Y |A
0
= a
0
, A
1
= a
1
, L
1
= l
1
] conditional on
the time-varying treatment and confounders required to achieve sequential ex-
changeability. The weights are the distribution of the confounder L
1
given the
past which, in this case, is the past value of treatment corresponding to the
intervention. Specifically, the g-formulaThe g-formula for time-varying
treatments was first described by
Robins (1986, 1987).
X
l
1
E [Y |A
0
= a
0
, A
1
= a
1
, L
1
= l
1
] f (l
1
|a
0
)
equals E [Y
a
0
,a
1
] under (static) sequential exchangeability for Y
a
0
,a
1
. That is,
for a time-varying treatment, the g-formula estimator of the counterfactual
mean outcome under the identifiability conditions is the mean outcome stan-
dardized to the distribution of the confounders in the study population, with
every factor in the expression conditional on past treatment and covariate his-
tory. This conditioning on prior history is not necessary in the time-fixed case
in which both treatment and confounders are measured at a single time point.
The g-formula is only computable (i.e., well-defined) if, for any value l
1
such that f (l
1
|a
0
) = 0, there are individuals with (A
0
= a
0
, A
1
= a
1
, L
1
= l
1
)
in the population. This is equivalent to the definition of positivity given in
Technical Point 19.2 and a generalization for time-varying treatments of the
discussion of positivity in Technical Point 3.1.
In a study with 2 time points, the
g-formula for “never treat” is
E [Y |A
0
= 0, A
1
= 0, L
1
= 0] ×
Pr [L
1
= 0|A
0
= 0] +
E [Y |A
0
= 0, A
1
= 0, L
1
= 1] ×
Pr [L
1
= 1|A
0
= 0]
Let us apply the g-formula to estimate the causal effect E
Y
a
0
=1,a
1
=1
−
E
Y
a
0
=0,a
1
=0
from the sequentially randomized experiment of Table 21.1.
The g-formula estimate for the mean E
Y
a
0
=0,a
1
=0
is 84×0.25+52×0.75 = 60.
The g-formula estimate for the mean E
Y
a
0
=1,a
1
=1
is 76×0.50+44×0.50 = 60.
Therefore the estimate of the causal effect E
Y
a
0
=1,a
1
=1
− E
Y
a
0
=0,a
1
=0
is
0, as expected. The g-formula succeeds where traditional methods failed.
Figure 21.1
Another way to think of the g-formula is as a simulation. Under sequential
exchangeability for Y and
¯
L jointly, the g-formula simulates the counterfac-
tual outcome Y
¯a
and covariate history
¯
L
¯a
that would have been observed if
everybody in the study population had followed treatment strategy ¯a. In other
21.1 The g-formula for time-varying treatments 273
words, the g-formula simulates (identifies) the joint distribution of the coun-
terfactuals
Y
¯a
,
¯
L
¯a
under strategy a. To see this, first consider the causally
interpreted structured tree graph in Figure 21.1, which is an alternative rep-
resentation of the data in Table 21.1. Under the aforementioned identifiability
condition, the g-formula can be viewed as a procedure to build a new tree in
which all individuals follow strategy ¯a. For example, the causally interpreted
structured tree graph in Figure 21.2 shows the counterfactual population that
would have been observed if all individuals have followed the strategy “always
treat” (a
0
= 1, a
1
= 1).
Figure 21.2
To simulate this counterfactual population we (i) assign probability 1 to
receiving treatment a
0
= 1 and a
1
= 1 at times k = 0 and k = 1, respectively,Under sequential exchangeabil-
ity, Pr [L
1
= l
1
|A
0
= a
0
] =
Pr
L
a=0
1
= l
1
and
E [Y |A
0
= a
0
, A
1
= a
1
, L
1
= l
1
] =
E [Y
a
0
,a
1
|L
a
0
1
= l
1
].
Thus the g-formula is
P
l
1
E [Y
a
0
,a
1
|L
a
0
1
= l
1
]
Pr [L
a
0
1
= l
1
], which equals
E [Y
a
0
,a
1
] as required.
and (ii) assign the same probability Pr [L
1
= l
1
|A
0
= a
0
] and the same mean
E [Y |A
0
= a
0
, A
1
= a
1
, L
1
= l
1
] as in the original study population.
Two important points. First, the value of the g-formula depends on what,
if anything, has been included in L. As an example, suppose we do not collect
data on L
1
because we believe, incorrectly, that our study is represented by
a causal diagram like the one in Figure 20.8 after removing the arrow from
L
1
to A
1
. Thus we believe L
1
is not a confounder and hence not necessary
for identification. Then the g-formula in the absence of data on L
1
becomes
E [Y |A
0
= a
0
, A
1
= a
1
] because there is no covariate history to adjust for. How-
ever, because our study is actually represented by the causal graph in Figure
20.8. (under which treatment assignment A
1
is affected by L
1
), the g-formula
that fails to include L
1
no longer has a causal interpretation.
Second, even when the g-formula has a causal interpretation, each of its
components may lack a causal interpretation. As an example, consider the
causal diagram in Figure 20.9 under which only static sequential exchangeabil-
ity holds. The g-formula that includes L
1
correctly identifies the mean of Y
a
.
Remarkably, regardless of whether we add arrows from A
0
and A
1
to Y , the g-
formula continues to have a causal interpretation as E [Y
¯a
], even though neither
of its components—E [Y |A
0
= a
0
, A
1
= a
1
, L
1
= l
1
] and Pr [L
1
= l
1
|A
0
= a
0
]—
has any causal interpretation at all. That is, Pr [L
1
= l
1
|A
0
= a
0
] = Pr [L
a
0
1
= l
1
]
and E [Y |A
0
= a
0
, A
1
= a
1
, L
1
= l
1
] = E [Y
a
0
,a
1
|L
a
0
1
= l
1
]. The last two in-
equalities will be equalities in a sequential randomized trial like the one repre-
sented in Figures 20.1 and 20.2.
274 G-methods for time-varying treatments
Fine Point 21.1
Treatment and covariate history When describing g-methods, we often refer to the treatment and covariate history
that is required to achieve sequential exchangeability. For the g-formula, we say that its components are conditional on
prior treatment and covariate history. For example, the factor corresponding to the probability of a discrete confounder
L
2
at time k = 2
f
l
2
|A
1
= ¯a
1
, L
1
=
¯
l
1
= Pr [L
2
= l
2
|A
0
= a
0
, A
1
= a
1
, L
0
= l
0
, L
1
= l
1
]
is conditional on treatment and confounders at prior times 0 and 1; the factor at time k = 3 is conditional on treatment
and confounders at times 0, 1, and 2, and so on.
However, the term “history” need not be defined temporally because, as explained in Fine Point 7.4, confounders
can theoretically be in the temporal future of a treatment. Conversely, as explained along with Figure 7.4, adjusting for
some variables in the temporal past of treatment may introduce selection bias (referred to as M-bias). Therefore, in
this book, the causally relevant “history” at time k should be understood as the set of treatments and confounders that
are needed to achieve conditional exchangeability for treatment A
k
. In most cases this use of history will correspond to
the chronological history.
Now let us generalize the g-formula to high-dimensional settings with mul-
tiple times k. The g-formula is
X
¯
l
E
Y |
¯
A = ¯a,
¯
L =
¯
l
K
Y
k=0
f
l
k
|¯a
k−1
,
¯
l
k−1
,
where the sum is over all possible
¯
l-histories (
¯
l
k−1
is the history through timeTechnical Point 21.1 shows a
more general expression for the g-
formula, which can be used to com-
pute densities, not just means.
k − 1). The sum
P
¯
l
can also be written as
P
l
K
...
P
l
1
P
l
0
. Under sequential
exchangeability for Y
¯a
given
¯
L
k
,
¯
A
k
at each time k, this expression equals
the counterfactual mean E [Y
¯a
] under treatment strategy ¯a. Fine Point 21.1
presents a more nuanced definition of the term “history”.
In practice, however, the components of the g-formula cannot be directly
computed if the data are high-dimensional, as is expected in observational stud-
ies with multiple confounders or time points. The quantities E
Y |
¯
A = ¯a,
¯
L =
¯
l
and f
l
k
|¯a
k−1
,
¯
l
k−1
will need to be estimated. For example, we can fit a lin-
ear regression model to estimate the conditional means E
Y |
¯
A = ¯a,
¯
L =
¯
l
of
the outcome variable at the end of follow-up, and logistic regression mod-
els to estimate the distribution of the discrete confounders L
k
at each time
k = 0 (the distribution of L
0
can be estimated without models as described
in Section 13.3). The estimates from these models,
b
E
Y |
¯
A = ¯a,
¯
L =
¯
l
and
b
f
l
k
|¯a
k−1
,
¯
l
k−1
, will then be plugged in into the g-formula. Since Chapter
13, we have referred to this estimator as the plug-in g-formula and, when the
estimates used in the plug-in g-formula are based on parametric models, we
have referred to the plug-in g-formula as the parametric g-formula.
For simplicity, this chapter largely focuses on the g-formula under determin-
istic strategies. However, under sequential exchangeability, the g-formula can
be used to compute the counterfactual mean of the outcome under a random
treatment strategy f
int
. An example of a random (static) strategy is “indepen-
dently at each time k, treat individuals with probability 0.3 and do not treat
with probability 0.7”, where f
int
1|¯a
k−1
,
¯
l
k
= 0.3. That is, f
int
a
k
|¯a
k−1
,
¯
l
k
is the conditional probability of treatment a
k
at time k under the treatment
21.1 The g-formula for time-varying treatments 275
Technical Point 21.1
The g-formula density The g-formula density for
Y, L
evaluated at
y,
¯
l
for a deterministic static strategy ¯a is
f
y|¯a
K
,
¯
l
K
K
Y
k=0
f
l
k
|¯a
k−1
,
¯
l
k−1
The static g-formula density for Y is simply the marginal density of Y under the g-formula density for
Y, L
:
Z
...
Z
f
y|¯a
K
,
¯
l
K
K
Y
k=0
dF
l
k
|¯a
k−1
,
¯
l
k−1
,
where the integral notation
R
is used to accommodate settings in which some components of L
k
are continuous.
The g formula density for
Y, L
and for Y for a dynamic deterministic strategy g = (g
0
, ..., g
K
), with g
k
a
k−1
, l
k
taking values in the support of A
k
, simply replaces a
k
by a
g
k
in the above formulae. Here, a
g
k
is recursively defined for
k = 0, ..., K, by a
g
k
≡ g
k
a
g
k−1
, l
k
≡
g
0
a
g
−1
, l
0
, ..., g
k
a
g
k−1
, l
k
with a
g
−1
defined to be 0. A static strategy is the
special case of a dynamic strategy when each g
k
a
k−1
, l
k
is a constant function.
In more generality, given observed data O =
¯
A, X, Y
and unobserved data U , where X is the set of all measured
variables other than treatment
¯
A and outcome Y , the inputs of the g-formula are (i) a deterministic treatment strategy
g, (ii) a causal DAG representing the observed data (and their unmeasured common causes), (iii) a subset L of X for
which we wish to adjust, and (iv) a choice of a total ordering of L,
¯
A, and Y consistent with the topology of the DAG,
i.e., an ordering such that each variable comes after its ancestors. The vector L
k
consists of all variables in L after
A
k−1
and before A
k
in the ordering. The chosen ordering will usually, but not always, be temporal as discussed in Fine
Point 21.1. When sequential exchangeability for Y
g
and positivity holds for the chosen ordering, the g-formula density
for Y equals the density f
Y
g
(y) that would have been observed in the study population if all individuals had followed
strategy g. Otherwise, the g-formula can still be computed, but it lacks a causal interpretation. When positivity and
exchangeability for
Y
g
, L
g
hold (e.g., no arrow from any variable either in U or in X but not in L directly into any
treatment variable), the g-formula density for
Y,
L
equals the density f
Y
g
,L
g
y,
l
.
strategy (or intervention) f
int
. Then, the general g-formula expression is
X
¯a,
¯
l
E
Y |
¯
A = ¯a,
¯
L =
¯
l
K
Y
k=0
f
l
k
|¯a
k−1
,
¯
l
k−1
K
Y
k=0
f
int
a
k
|¯a
k−1
,
¯
l
k
.
Note this is the formula for the observed mean of Y if we replace f
int
a
k
|¯a
k−1
,
¯
l
k
by the observed conditional probability of treatment f
a
k
|¯a
k−1
,
¯
l
k
.
This expression of the g-formula is general enough to accommodate both
deterministic and random strategies. Under a deterministic treatment strategy,code: The gfoRmula R pack-
age (Lin et al. 2019) is available
through CRAN. The GFORMULA
SAS macro is available through
GitHub. See the book’s web site.
f
int
a
k
|¯a
k−1
,
¯
l
k
is always 1 for the values of a
k
mandated by the strategy
and 0 for the others. For example, under the strategy “never treat” or ¯a =
(0, 0, ...0), the probability f
int
0|¯a
k−1
,
¯
l
k
= 1 at all k. Since f
int
a
k
|¯a
k−1
,
¯
l
k
equals 1 for the mandated values of treatment and 0 for all other values of
treatment, it is not necessary to include the f
int
factors, or the sum over ¯a,
in the above formula. Our publicly available software implements this general
expression of the g-formula and therefore can accommodate any treatment
strategy.
276 G-methods for time-varying treatments
21.2 IP weighting for time-varying treatments
Suppose we are only interested in the effect of the time-fixed treatment A
1
in Table 21.1. We then want to contrast the counterfactual mean outcomes
E
Y
a
1
=1
and E
Y
a
1
=0
. As we have seen in Chapter 12, under the iden-
tifiability conditions, each of the counterfactual means E [Y
a
1
] is the mean
E
ps
[Y |A
1
= a
1
] in the pseudo-population created by the subject-specific non-
stabilized weights W
A
1
= 1/f (A
1
|L
1
) or the stabilized weights SW
A
1
=
f (A
1
) /f (A
1
|L
1
). The denominator of the IP weights is, informally, an individ-
ual’s probability of receiving the treatment value that he or she received, condi-
tional on the individual’s confounder values. One can estimate E
ps
[Y |A
1
= a
1
]
from the observed study data by the average of Y among subjects with A
1
= a
1
in the pseudo-population.
When treatment and confounders are time-varying, these IP weights for
time-fixed treatments need to be generalized. For a time-varying treatment
A = (A
0
, A
1
) and time-varying covariates
¯
L = (L
0
, L
1
) at two time points, the
nonstabilized IP weights are
W
¯
A
=
1
f (A
0
|L
0
)
×
1
f (A
1
|A
0
, L
0
, L
1
)
=
1
Y
k=0
1
f
A
k
|
¯
A
k−1
,
¯
L
k
and the stabilized IP weights are
SW
¯
A
=
f (A
0
)
f (A
0
|L
0
)
×
f (A
1
|A
0
)
f (A
1
|A
0
, L
0
, L
1
)
=
1
Y
k=0
f
A
k
|
¯
A
k−1
f
A
k
|
¯
A
k−1
,
¯
L
k
where A
−1
is 0 by definition. The denominator of the IP weights for a time-
varying treatment is, informally, an individual’s probability of receiving the
treatment history that he or she received, conditional on the individual’s treat-
ment and covariate history.
Suppose we want to contrast the counterfactual means E
Y
a
0
=1,a
1
=1
and
E
Y
a
0
=0,a
1
=0
. Under the identifiability assumptions for static strategies,
each counterfactual mean E [Y
a
0
,a
1
] is the mean E
ps
[Y |A
0
= a
0
, A
1
= a
1
] in
the pseudo-population created by the nonstabilized weights W
¯
A
or the stabi-
lized weights SW
¯
A
. That is, the IP weighted estimator of each counterfactualSimilar to the result for time-fixed
treatment in Technical Point 12.2,
E
ps
[Y |A
0
= a
0
, A
1
= a
1
] equals
E
h
W
¯
A
Y I (A
0
= a
0
, A
1
= a
1
)
i
=
E
[
SW
¯
A
Y I(A
0
=a
0
,A
1
=a
1
)
]
E
[
SW
¯
A
I(A
0
=a
0
,A
1
=a
1
)
]
, for both
the nonstabilized and stabilized
pseudo-populations, regardless of
whether sequential exchangeability
holds.
mean is the average of Y among individuals with A = (A
0
, A
1
) in the pseudo-
population.
Let us apply IP weighting to the data from Table 21.1. The causally in-
terpreted structured tree graph in Figure 21.3 is the tree graph in Figure 21.1
with additional columns for the nonstabilized IP weights W
¯
A
and the number
of individuals in the corresponding pseudo-population N
W
for each treatment
and covariate history. The pseudo-population has a size of 128, 000, i.e., the
32, 000 individuals in the original population multiplied by 4, the number of
static strategies. Because there is no L
0
in this study, the denominator of the
IP weights simplifies to f (A
0
) f (A
1
|A
0
, L
1
).
The IP weighted estimator for the counterfactual mean E
Y
a
0
=0,a
1
=0
is
the mean E
ps
[Y |A
0
= 0, A
1
= 0] in the pseudo-population, which we estimate
as the average outcome among the 32, 000 individuals with (A
0
= 0, A
1
= 0) in
the pseudo-population. From the tree in Figure 21.3, the estimate is 84×
8000
32000
+
52 ×
24000
32000
= 60. Similarly, the IP weighted estimate of E
Y
a
0
=1,a
1
=1
is also
60. Therefore the estimate of the causal effect E
Y
a
0
=1,a
1
=1
−E
Y
a
0
=0,a
1
=0
is 0, as expected. IP weighting, like the g-formula, succeeds where traditional
methods failed.
21.2 IP weighting for time-varying treatments 277
Note that our nonparametric estimates of E [Y
a
0
,a
1
] based on the g-formula
are precisely equal to those based on IP weighting. This equality has nothingThe same estimate of 0 is obtained
when using stabilized weights SW
¯
A
in Figure 21.3 (check for yourself).
However, Pr
ps
A
k
= 1|
¯
A
k−1
,
¯
L
k
is 1/2 in the nonstabi-
lized pseudo-population and
Pr
ps
A
k
= 1|
¯
A
k−1
in the stabi-
lized pseudo-population.
to do with causal inference. That is, even if the identifiability conditions did
not hold—so neither the g-formula nor IP weighting estimates have a causal
interpretation—both approaches would yield the same number.
Figure 21.3
Let us generalize IP weighting to high-dimensional settings with multiple
times k = 0, 1...K. The general form of the nonstabilized IP weights is
W
¯
A
=
K
Y
k=0
1
f
A
k
|
¯
A
k−1
,
¯
L
k
and the general form of the stabilized IP weights is
SW
¯
A
=
K
Y
k=0
f
A
k
|
¯
A
k−1
f
A
k
|
¯
A
k−1
,
¯
L
k
When the identifiability conditions hold, these IP weights create a pseudo-
population in which (i) the mean of Y
¯a
is identical to that in the actual pop-
ulation, but (ii) like on Figure 19.1, the randomization probabilities at each
time k are the constant 1/2 (nonstabilized weights) or depend at most on
past treatment history (stabilized weights). Hence the average causal effect
E [Y
¯a
] −E
h
Y
¯a
′
i
is E
ps
Y |A = ¯a
−E
ps
Y |A = ¯a
′
because sequential uncon-Our description in the text con-
siders only static strategies. For
a description of IP weighting with
dynamic strategies, see Technical
Point 21.2.
ditional exchangeability holds in both pseudo-populations.
In a true sequentially randomized trial, the quantities f
A
k
|
¯
A
k−1
,
¯
L
k
are
known by design. Therefore we can use them to compute nonstabilized IP
weights and the estimates of E [Y
¯a
] and E [Y
¯a
] −E
h
Y
¯a
′
i
are guaranteed to be
unbiased. In contrast, in observational studies, the quantities f
A
k
|
¯
A
k−1
,
¯
L
k
will need to be estimated from the data. When the data are high-dimensional,
we can, for example, fit a logistic regression model to estimate the condi-
tional probability of a dichotomous treatment Pr
A
k
= 1|
¯
A
k−1
,
¯
L
k
at each
time k. The estimates
b
f
A
k
|
¯
A
k−1
,
¯
L
k
from these models will then replace
f
A
k
|
¯
A
k−1
,
¯
L
k
in W
¯
A
. If the estimates
b
f
A
k
|
¯
A
k−1
,
¯
L
k
are based on a mis-
specified logistic model for the Pr
A
k
= 1|
¯
A
k−1
,
¯
L
k
, the resulting estimates of
278 G-methods for time-varying treatments
Technical Point 21.2
IP weighting for dynamic treatment strategies. Consider the deterministic dynamic strategy g = (g
0
, ..., g
K
) with
g
k
≡ g
k
a
k−1
, l
k
. The g-formula for an outcome Y under g equals E
h
Y I(
¯
A
K
= A
g
K
)W
¯
A
i
, where a
g
K
was de-
fined in Technical Point 21.1. Further, E
h
Y I(
¯
A
K
= A
g
K
)W
¯
A
i
= E
ps
[Y |
¯
A
K
= A
g
K
] where E
ps
[Y |
¯
A
K
= A
g
K
] is
the mean of Y among the members of the pseudo-population who follow strategy g. Unlike for static strategies,
E
h
Y I(
¯
A
K
= A
g
K
)SW
¯
A
i
/ E
h
I(
¯
A
K
= A
g
K
)SW
¯
A
i
does not equal the g-formula because the numerator of SW
¯
A
de-
pends on A. Hence stabilized weights cannot be used with dynamic strategies. For a random dynamic strategy f
int
,
the g-formula is equal to E
Y
K
Q
k=0
f
int
A
k
|
¯
A
k−1
,
¯
L
k
W
¯
A
= E
Y
K
Q
k=0
f
int
(
A
k
|
¯
A
k−1
,
¯
L
k
)
f
(
A
k
|
¯
A
k−1
,
¯
L
k
)
.
E [Y
¯a
] and E [Y
¯a
]−E
h
Y
¯a
′
i
will be biased. For stabilized weights SW
¯
A
we mustIn practice, a common approach
is to fit a single model for
Pr
A
k
= 1|
¯
A
k−1
,
¯
L
k
rather than
a separate model at each time k.
The model includes functions of
time k—a time-varying intercept—
as covariates, and possibly product
terms with other covariates.
also obtain an estimate of
b
f
A
k
|
¯
A
k−1
for the numerator. Even if this estimate
is based on a misspecified model, the estimates of E [Y
¯a
] and E [Y
¯a
] −E
h
Y
¯a
′
i
remain unbiased, although
b
f (a
k
|a
k−1
) in the stabilized pseudo-population will
no longer be consistent for the observed data density f (a
k
|a
k−1
).
Suppose that we obtain two estimates of E [Y
¯a
], one using the parametric
g-formula and another one using IP weights estimated via parametric models,
and that the two estimates differ by more than can be reasonably explained by
sampling variability (the sampling variability of the difference of the estimates
can be quantified by bootstrapping). We can then conclude that the parametricThere is no logical guarantee of no
model misspecification even when
the estimates from both paramet-
ric approaches are similar, as they
may both be biased in the same di-
rection.
models used for the g-formula or the parametric models used for IP weighting
(or both) are misspecified. This conclusion is always true, regardless of whether
the identifiability assumptions hold. An implication is that one should always
estimate E [Y
¯a
] using both methods and, if the estimates differ substantially
(according to some prespecified criterion), reexamine all the models and modify
them where necessary. In the next section, we describe how doubly-robust
estimators can help deal with model misspecification.
Also, as we discussed in the previous section, it is not infrequent that the
number of unknown quantities E [Y
¯a
] far exceeds the sample size. Thus we
need to specify a model that combines information from many strategies to
help estimate a given E [Y
¯a
]. For example, we can hypothesize that the effect
of treatment history ¯a on the mean outcome increases linearly as a function of
the cumulative treatment cum (¯a) =
K
P
k=0
a
k
under strategy ¯a. This hypothesis
is encoded in the marginal structural mean modelThis marginal structural model is
unsaturated. Remember, saturated
models have an equal number of
unknowns on both sides of the
equation.
E
Y
¯a
= β
0
+ β
1
cum (¯a)
for all a, which is a more general version of the marginal structural mean model
for time-fixed treatments discussed in Chapter 12. There are 2
K
different
unknown quantities on the left hand side of model, one for each of the 2
K
different strategies ¯a, but only 2 unknown parameters β
0
and β
1
on the right
hand side. The parameter β
1
measures the average causal effect of the time-
varying treatment
¯
A. The average causal effect E [Y
¯a
] − E
h
Y
¯a=0
i
is equal to
β
1
× cum (¯a).
As discussed in Chapter 12, to estimate the parameters of the marginal
21.2 IP weighting for time-varying treatments 279
structural model, we can fit the linear regression model
E
Y |A
= θ
0
+ θ
1
cum
A
by ordinary least squares in either the stabilized or nonstabilized pseudo-In statistics courses, it is often
proven that, under a correctly spec-
ified model for E
Y |A
, both ordi-
nary and weighted least squares es-
timates are consistent for the asso-
ciational parameter θ
1
. This proof
assumes that the weights only de-
pend on A. When, as in our case,
the weights depend on covariates L
that are correlated with Y given A,
the weighted regression is no longer
consistent for θ
1
.
population. This is mathematically equivalent to fitting the same linear model
by weighted least squares in the original study population, with weights SW
¯
A
or W
¯
A
, respectively (in an actual data analysis, these weights are replaced
by their estimates). Under the identifiability conditions, the weighted least
squares estimate of θ
1
is consistent for the causal parameter β
1
rather than for
the associational parameter θ
1
.
As also discussed in Chapter 12, the variance of
b
β
1
—and thus of the con-
trast E [Y
¯a
] −E
h
Y
¯a=0
i
—can be estimated by the nonparametric bootstrap or
by computing its analytic variance (which requires additional statistical anal-
ysis and programming). We can also construct a conservative 95% confidence
interval by using the robust variance estimator of
b
β
1
, which is directly out-
putted by most statistical software packages. For a non-saturated marginal
structural model the width of the intervals will typically be narrower when the
model is fit with the weights SW
¯
A
than with the weights W
¯
A
, so the SW
¯
A
weights are preferred.
Of course, the estimates of E [Y
¯a
] will be incorrect if the marginal struc-
tural mean model is misspecified, that is, if the mean counterfactual outcome
depends on the treatment strategy through a function of the time-varying treat-
ment other than cumulative treatment cum (¯a) (say, cumulative treatment only
in the final 5 months
K
P
k=K−5
a
k
) or depends nonlinearly (say, quadratically) on
cumulative treatment. However, if we fit the model
E
Y |A
= θ
0
+ θ
1
cum
A
+ θ
2
cum
−5
A
+ θ
3
cum
A
2
with weights SW
¯
A
or W
¯
A
, a Wald test on two degrees of freedom of the joint
hypothesis θ
2
= θ
3
= 0 is a test of the null hypothesis that our marginal struc-This test will generally have good
statistical power against the partic-
ular directions of misspecification
mentioned above, especially when
using the weights SW
¯
A
and the
bootstrap to estimate the variance.
tural model is correctly specified. That is, IP weighting of marginal structural
models is not subject to the g-null paradox described in Technical Point 21.3.
In practice, one might choose to use a marginal structural model that includes
different summaries of treatment history A as covariates, and that uses flexible
functions like, say, cubic splines.
Finally, as we discussed in Section 12.5, we can use a marginal structural
model to explore effect modification by a subset V of the covariates in L
0
.
For example, for a dichotomous baseline variable V , we would elaborate our
marginal structural mean model as
E
Y
¯a
|V
= β
0
+ β
1
cum (¯a) + β
2
V + β
3
cum (¯a) V
The parameters of this model can be estimated by fitting the ordinary linear
regression model E
Y |A, V
= θ
0
+θ
1
cum
A
+θ
2
V +θ
3
V cum
A
by weighted
least squares with IP weights W
¯
A
or, better, SW
¯
A
(V ) =
K
Y
k=0
f
A
k
|
¯
A
k−1
, V
f
A
k
|
¯
A
k−1
,
¯
L
k
.
In the presence of treatment-confounder feedback, V can only include baseline
variables. If V had components of L
k
for k > 0 then the parameters θ
1
and θ
3
could be different from 0 even if treatment had no effect on the mean outcome
at any time.
We now describe a doubly robust estimator of the counterfactual mean
E [Y
g
] for any strategy g.
280 G-methods for time-varying treatments
Technical Point 21.3
The g-null paradox. When using the parametric g-formula, model misspecification will result in biased estimates of
E [Y
¯a
], even if the identifiability conditions hold. Suppose there is treatment-confounder feedback and the sharp null
hypothesis of no effect of treatment on Y is true, i.e.,
Y
¯a
− Y
¯a
′
= 0 with probability 1 for all ¯a
′
and ¯a.
Then the value of the g-formula for E [Y
¯a
] is the same for any strategy ¯a, even though E
Y |
¯
A = ¯a,
¯
L =
¯
l
and
f
l
k
|¯a
k−1
,
¯
l
k−1
will both depend on ¯a as discussed in Chapter 20. Now suppose we use standard non-saturated para-
metric models E
Y |
¯
A = ¯a,
¯
L =
¯
l; θ
and f
l
k
|¯a
k−1
,
¯
l
k−1
; φ
based on distinct (i.e., variation-independent) parameters
θ and φ to estimate the components of the g-formula. Then Robins and Wasserman (1997) showed that, when L
k
has
any discrete components, these models cannot all be correctly specified because the estimated value of the g-formula for
E [Y
¯a
] will generally depend on ¯a. As a consequence, inference based on the estimated g-formula might theoretically re-
sult in the sharp null hypothesis being falsely rejected, even in a sequentially randomized experiment. This phenomenon
is referred to as the null paradox of the estimated g-formula for time-varying treatments. For additional discussion, see
Cox and Wermuth (1999) and McGrath et al. (2022). Fortunately, the g-null paradox has not prevented null parametric
g-formula effect estimates in practice, presumably because the bias induced by the paradox is small compared with
typical random variability.
In contrast, as described in Chapters 12 and 14, neither IP weighting of marginal structural mean models nor g-
estimation of structural nested mean models suffer from the null paradox. These models are correctly specified under
the sharp null no matter what functional form we choose for treatment. For example, the marginal structural mean
model E [Y
¯a
] = β
0
+ β
1
cum (¯a) is correctly specified under the null because, in that case, β
1
= 0 and E [Y
¯a
] would
not depend on the function of ¯a. Also, as defined in Section 21.4, any structural nested mean model γ
k
a
k−1
, l
k
, β
is
correctly specified under the sharp null with β = 0 being the true parameter value and γ
k
a
k−1
, l
k
, β
= 0, regardless
of the function of past treatment and covariate history.
21.3 A doubly robust estimator for time-varying treatments
Part II briefly mentioned doubly robust methods that combine IP weighting
and the g-formula. As we know, IP weighting requires a correct model for treat-
ment A conditional on the confounders L, and the g-formula requires a correct
model for the outcome Y conditional on treatment A and the confounders L.
Doubly robust methods require a correct model for either treatment A or out-
come Y . If at least one of the two models is correct (and one need not know
which of the two models is correct), a doubly robust estimator consistently
estimates the causal effect. Fine Point 13.2 described a doubly robust plug-Doubly robust estimators give us
two chances to get it right when,
as in most observational studies,
there are many confounders and
non-saturated models are required.
in estimator for the average causal effect of a time-fixed treatment A on an
outcome Y . In this section, we first review a slightly different doubly robust
plug-in estimator for time-fixed treatments and then extend it to time-varying
treatments.
Suppose we want to construct a doubly robust estimator of the average
causal effect E
Y
a=1
− E
Y
a=0
of a time-fixed binary treatment A on a
binary outcome Y under exchangeability, positivity, and consistency in a set-
ting with many confounders L. We will construct doubly robust estimators of
E [Y
a
] as previously discussed in Technical Points 13.2 and 13.3. The difference
between doubly robust estimators for E
Y
a=1
and for E
Y
a=0
is a doubly
robust estimator of the average causal effect. Our doubly robust procedure for
E [Y
a
] will use estimates of an outcome model for E[Y |A = a, L = l] and a
model for Pr[A = 1|L] and then combine them appropriately. Our procedure
has three steps.
21.3 A doubly robust estimator for time-varying treatments 281
The first step is to compute the predicted values
b
f(a|L) ≡
c
Pr [A = a|L]
from the treatment model. The second step is to compute the predicted values
b
E [Y |A = a, L] = b
a, L;
b
θ
from the maximum likelihood fit restricted to in-
dividuals with A = a of the linear logistic model b (a, L; θ) that includes
ˆ
W
a
=
1/
b
f(a|L) as a covariate, such as b (a, L; θ) = expit
θ
a,0
+ θ
a,1
L + θ
a,2
ˆ
W
a
.
The third step is to estimate E
Y
a=1
and E
Y
a=0
as the standardized means
b
E
h
b
1, L;
b
θ
i
and
b
E
h
b
0, L;
b
θ
i
, where
b
E denotes the sample average over
all individuals, both treated and untreated. The difference
b
E
h
b
1, L;
b
θ
i
−
b
E
h
b
0, L;
b
θ
i
is a doubly robust estimator of the causal effect E
Y
a=1
−
E
Y
a=0
. That is, under the identifiability conditions, this estimator consis-
tently estimates the average causal effect if either the model for the treatment
is correct or the models for the outcome are correct. It is important to realize
that treated and untreated individuals with the same value of L also have the
same value of b
1, L;
b
θ
= expit
b
θ
1,0
+
b
θ
1,1
L +
b
θ
1,2
/
b
f(a = 1|L)
. They also
have the same value of b
0, L;
b
θ
= expit
b
θ
0,0
+
b
θ
0,1
L +
b
θ
0,2
/
b
f(a = 0|L)
.
Let us now extend this doubly robust estimator to settings with time-
varying treatments in which we are interested in comparing the counterfactual
means E [Y
¯a
] and E
h
Y
¯a
′
i
under two treatment strategies ¯a and ¯a
′
. The doublyThis doubly robust estimator is due
to Bang and Robins (2005) and is
closely related to an earlier estima-
tor (Robins, 2000). The estimator
is a targeted minimum loss-based
estimator (TMLE), also known as
a targeted maximum likelihood es-
timator, in the nomenclature later
introduced by van der Laan and Ru-
bin (2006) and van der Laan and
Gruber (2012).
robust procedure to estimate E [Y
¯a
] for a time-varying treatment follows the
same 3 steps as the procedure to estimate E [Y
a
] for a time-fixed treatment.
However, as we will see, the second step is a bit more involved because it
requires the fitting of sequential regression models. To simplify notation, we
show how to obtain a doubly robust estimator of E [Y
¯a
] under the treatment
strategy “always treated”, i.e., ¯a = 1 where 1 = 1
K
is the vector of K + 1 1’s.
The first step requires fitting a regression model π
k
¯
L
k
; α
for π
k
¯
L
k
=
Pr
A
k
= 1|
¯
A
k−1
= 1
k−1
,
¯
L
k
pooled over all persons and times k. An indi-
vidual contributes to the fit of the model at time k only if the individual
has been treated (continuously) through k − 1, i.e.,
¯
A
k−1
= 1
k−1
. We then
use predicted values π
k
¯
L
k
; bα
from this model to estimate for those indi-
viduals treated through m (
¯
A
m
= 1
m
), the time-varying IP weights W
A
m
=
Q
m
k=0
1
f
A
k
|
¯
A
k−1
,
¯
L
k
which equals W
1
m
=
Q
m
k=0
1
π
k
(
¯
L
k
)
. That is, for an
always-treated individual with
¯
A
K
= 1
K
, we assign a different weight W
1
m
for each time point m rather than just the single weight W
1
K
at the end of
follow-up as we did in the previous section. For example, if we fit the para-
metric model π
k
¯
L
k
; α
= expit (α
0,k
+ α
2
L
k
) for Pr
A
k
= 1|
¯
A
k−1
= 1,
¯
L
k
,
then, in our example of Table 21.1 with two time points (K = 1), the predicted
values
c
Pr
A
1
= 1|A
0
= 1,
¯
L
1
and
c
Pr [A
0
= 1|L
0
] are bπ
1
= expit (ˆα
0,1
+ ˆα
2
L
1
)
and bπ
0
= expit (ˆα
0,0
+ ˆα
2
L
0
) (because A
−1
≡ 0). Here, we used the abbrevia-
tion bπ
k
for π
k
¯
L
k
; bα
. We then compute the time-varying IP weight estimates
ˆ
W
1
m
=
Q
m
k=0
1
bπ
k
for individuals treated through m. We have reached the end
of Step 1.
The second step requires fitting a separate outcome model b
m
¯
L
m
; β
m
at
each time m, starting from the last time K and ending at m = 0. The time
m regression model is only fit to individuals treated through m and includes
ˆ
W
1
m
=
ˆ
W
A
m
as a covariate. The time K model has dependent variable Y . The
time m model for m < K has as dependent variable the predicted outcomes
from the fit of the time m + 1 model, i.e.,
b
B
m+1
=
b
b
m+1
¯
L
m+1
; β
m+1
. When
282 G-methods for time-varying treatments
Technical Point 21.4
A K+2 robust augmented IP weighted estimator. We consider the case K = 1 as the argument generalizes to
arbitrary K. The ICE plug-in estimator of the g-formula ψ is
b
ψ
gfor
= P
n
[
b
b
0
(L
0
)], where P
n
denotes a sample average,
b
b
0
(L
0
) =
b
E[
b
b
1
(L
0
, L
1
)|A
0
= 1, L
0
], and
b
b
1
(L
0
, L
1
) =
b
E[Y |L
0
, A
0
= 1, L
1
, A
1
= 1]. The IP weighted estimator
b
ψ
IP W
of ψ is P
n
[A
0
A
1
Y/(bπ
0
bπ
1
))] where bπ
0
and bπ
1
are estimates of π
0
= Pr(A
0
= 1|L
0
) and π
1
= Pr(A
1
= 1 |L
0
, L
1
, A
0
=
1). Robins et al. (1994) derived an augmented IP weighted estimator
b
ψ
T R
= P
n
[
b
U
T R
] of ψ where
b
U
T R
= A
0
A
1
Y/(bπ
0
bπ
1
) −
A
0
bπ
0
{
A
1
bπ
1
− 1}
b
b
1
(L
0
, L
1
) − {
A
0
bπ
0
− 1}
b
b
0
(L
0
)
We now show that
b
ψ
T R
is triply (i.e., K + 2) robust. First,
b
ψ
T R
is consistent (singly robust) for ψ if bπ
0
and bπ
1
are
consistent since the sample averages of the last 2 terms of
b
U
T R
are then consistent for 0 and the sample average of the first
term is precisely
b
ψ
IP W
. Second,
b
ψ
T R
is doubly robust because
b
ψ
T R
is consistent when
b
E[Y |L
0
, A
0
= 1, L
1
, A
1
= 1]
and
b
E[b
1
(L
0
, L
1
) |A
0
= 1, L
0
] are consistent for E(Y |L
0
, A
0
= 1, L
1
, A
1
= 1) and E[b
1
(L
0
, L
1
) |A
0
= 1, L
0
]. Here
b
E[b
1
(L
0
, L
1
) |A
0
= 1, L
0
] applies the same regression algorithm to the true b
1
(L
0
, L
1
) as was applied to
b
b
1
(L
0
, L
1
) to
obtain
b
b
0
(L
0
). To see this, we arrange terms to obtain
b
U
T R
=
b
b
0
(L
0
)+
A
0
A
1
bπ
0
bπ
1
(Y −
b
b
1
(L
0
, L
1
))+
A
0
bπ
0
(
b
b
1
(L
0
, L
1
)−
b
b
0
(L
0
)).
The sample averages of the last 2 terms are consistent for 0 and the sample average of the first term is
b
ψ
gfor
. Third,
b
ψ
T R
is triply robust because it is consistent if both
b
b
1
(L
0
, L
1
) and bπ
0
are consistent (Molina et al. 2017). This follows
because
b
U
T R
can be rewritten as A
0
b
b
1
(L
0
, L
1
)/bπ
0
+
A
0
A
1
bπ
0
bπ
1
(Y −
b
b
1
(L
0
, L
1
)) −
A
0
bπ
0
− 1
b
b
0
(L
0
). Hence, the sample
average of the last 2 terms converges to zero and the sample average of the first converges to E[b
0
(L
0
)]. However it
is not consistent when only bπ
1
and
b
E[b
1
(L
0
, L
1
) |A
0
= a
0
, L
0
] are consistent.
By modifying our estimator
b
ψ
T R
we can construct a quadruply robust (i.e., 2
K+1
) estimator
b
ψ
QR
that is consistent
when only bπ
1
and
b
E[b
1
(L
0
, L
1
) |A
0
= a
0
, L
0
] are consistent (Tchetgen Tchetgen 2009). Let
e
b
0
(L
0
) =
b
E
A
1
Y
bπ
1
−
A
1
bπ
1
− 1
b
b
1
(L
0
, L
1
) |A
0
= 1, L
0
Then
b
ψ
QR
= P
n
[
b
U
QR
], where
b
U
QR
is
b
U
T R
except with
b
b
0
(L
0
) replaced by
e
b
0
(L
0
). The advantage of
e
b
0
(L
0
) over
b
b
0
(L
0
) is that
e
b
0
(L
0
) is itself doubly robust in the sense that it is consistent for b
0
(L
0
) = E[b
1
(L
0
, L
1
) |A
0
= 1, L
0
]
if
b
E[b
1
(L
0
, L
1
) |A
0
= 1, L
0
] is consistent for b
0
(L
0
) and either bπ
1
or
b
b
1
(L
0
, L
1
) =
b
E[Y |L
0
, A
0
= 1, L
1
, A
1
= 1] are
consistent, which implies that
b
ψ
QR
is quadruply robust.
we reach the predicted value
b
B
0
= b
0
¯
L
0
;
b
β
we have completed step 2.For a binary Y , we could fit
a logistic model b
m
¯
L
m
; β
m
=
expit
h
γ
m
X
m
+ ς
m
ˆ
W
1
m
i
; X
m
is a
vector function of covariates
¯
L
m
and β
m
= (γ
m
, ς
m
). Even though
b
B
K
is not a whole number, it is
guaranteed to be in [0,1] and thus
can be used as the outcome variable
in a logistic model. For a continu-
ous Y , we could fit a linear regres-
sion model γ
m
X
m
+ ς
m
ˆ
W
1
m
.
In step 3 we compute our estimate of
b
E
h
Y
¯a=1
i
as the sample average over
all individuals of
b
B
0
. If (i) the outcome models b
m
¯
L
m
; β
m
are correctly spec-
ified for all m, or (ii) the treatment models π
k
¯
L
k
; α
are correctly specified
for all m, then
b
E
h
Y
¯a=1
i
will be (asymptotically) unbiased for E
h
Y
¯a=1
i
. In
that case,
b
E
h
Y
¯a=1
i
is said to be doubly robust. However,
b
E
h
Y
¯a=1
i
is actually
multiply robust since it is also (asymptotically) unbiased for E
h
Y
¯a=1
i
if, for
any m ∈ {0, 1, .., K − 1}, the treatment model is correct for times 0 to m and
the outcome model is correct for times m + 1 to K. We refer to this prop-
erty of the estimator as K + 2 robustness. In Technical Points 21.4 and 21.5,
we explain why these robustness properties are true and we show there exist
estimators with even better robustness properties than
b
E
h
Y
¯a=1
i
. In fact, we
21.4 G-estimation for time-varying treatments 283
Technical Point 21.5
A plug-in K+2 robust estimator. A potential drawback of the estimator
b
ψ
T R
of Technical Point 21.12 was that,
for binary Y ,
b
ψ
T R
could lie outside the support [0, 1] of ψ in a given sample. In contrast,
b
ψ
gfor
= P
n
h
b
b
0
(L
0
)
i
is
a plug-in estimator of ψ and always lies within [0, 1] if one estimates E[Y |L
0
, A
0
= a
0
, L
1
, A
1
= a
1
] and b
0
(L
0
) =
E[b
1
(L
0
, L
1
) |A
0
= a
0
, L
0
] using (parametric or nonparametric) logistic regression models. One obtains a plug-in
estimator
b
ψ
T R,plug
= P
n
h
b
b
0
(L
0
)
i
that is also triply robust if, for
b
U
T R
=
b
b
0
(L
0
) +
A
0
A
1
bπ
0
bπ
1
(Y −
b
b
1
(L
0
, L
1
)) +
A
0
bπ
0
(
b
b
1
(L
0
, L
1
) −
b
b
0
(L
0
))
it can be guaranteed that P
n
h
A
0
A
1
bπ
0
bπ
1
(Y −
b
b
1
(L
0
, L
1
))
i
and P
n
h
A
0
bπ
0
(
b
b
1
(L
0
, L
1
) −
b
b
0
(L
0
))
i
are both zero in every sample.
For example, one achieves P
n
h
A
0
A
1
bπ
0
bπ
1
(Y −
b
b
1
(L
0
, L
1
))
i
= 0 by including a univariate term θ
1
n
A
0
A
1
bπ
0
bπ
1
o
in a linear
logistic model for b
1
(L
0
, L
1
) = E [Y |L
0
, A
0
= 1, L
1
, A
1
= 1] with dependent variable Y fit by maximum likelihood to
individuals with A
0
= A
1
= 1. One next achieves P
n
h
A
0
bπ
0
(
b
b
1
(L
0
, L
1
) −
b
b
0
(L
0
))
i
= 0 by including a term θ
0
A
0
bπ
0
in a
logistic model for b
0
(L
0
) ≡ E[b
1
(L
0
, L
1
) |A
0
= a
0
, L
0
] with dependent variable
b
b
1
(L
0
, L
1
) fit by maximizing a logistic
likelihood to individuals with A
0
= 1. The estimator
b
E[Y
a=1
] given in the main text is an instance of
b
ψ
T R,plug
.
exhibit an estimator of E
h
Y
¯a=1
i
that is 2
K+1
robust.Molina et al. (2017) noted that
this estimator was actually K + 2
robust. Rotnitzky et al. (2017)
studied the asymptotic bias of this
and other multiply robust estima-
tor when using nonparametric and
machine learning estimators of the
treatment and outcome regression
functions.
To estimate the counterfactual mean E
h
Y
¯a=0
i
under the treatment strat-
egy “never treated”, repeat the above steps using ¯a = 0 where a = 0
K
is the
vector of K + 1 0’s. The difference of means estimated under each strategy is
a multiply robust estimator of the average causal effect E
h
Y
¯a=1
i
−E
h
Y
¯a=0
i
.
The multiply robust estimator described here can only be used to estimate
the counterfactual mean E [Y
¯a
] under a static treatment strategy ¯a. Technical
Point 21.6 describes a multiply robust estimator for the counterfactual mean
E [Y
g
] under a treatment strategy g that can be either static or dynamic and
either deterministic or random. This estimator is sometimes referred to as a
targeted minimum loss-based estimator (TMLE).
The implementation of multiply robust estimators has been historically
hampered by computational constraints and lack of user-friendly software, es-
pecially for hazards-based survival analysis. We anticipate that, in the near
future, software will become available and these multiply robust estimators (fit
using machine learning and sample splitting) will become more common when
studying the effect of complex treatment strategies on failure time outcomes.
See Fine Point 21.2 for a description of the different representations of the
g-formula and their connections to the above estimator.
21.4 G-estimation for time-varying treatments
If we were only interested in the effect of the time-fixed treatment A
1
in Table
21.1, we might have recourse to structural nested mean models for the condi-
tional causal effect of a time-fixed treatment within levels of the covariates, as
described in Chapter 14. Those models had a single equation because there was
284 G-methods for time-varying treatments
Technical Point 21.6
A multiply robust estimator. Let f
g
a
m
|a
m−1
, l
m
denote the treatment density at time m under strat-
egy g. For a static a
∗
, f
g
a
m
|a
m−1
, l
m
= I (a
m
= a
∗
m
); for a deterministic dynamic g, f
g
a
m
|a
m−1
, l
m
=
I
a
m
= g
m
a
m−1
, l
m
; and for a random dynamic f
int
, f
g
a
m
|a
m−1
, l
m
= f
int
a
m
|a
m−1
, l
m
. Let C
g
k
=
I
Q
k
m=0
f
g
A
m
|A
m−1
, L
m
= 0
equal 0 if an individual’s observed treatment history A
k
is compatible with g and 1
otherwise. The following algorithm computes a multiply robust plug-in estimator
b
ψ
dr,plug
of ψ = E [Y
g
] based on one
proposed by Rotnitzky et al. (2017), which is closely related to estimators by Robins (2000), Bang and Robins (2005),
van der Laan and Gruber (2012), and Petersen et al. (2014).
1. Fit models f
m
a
m
|a
m−1
, l
m
; α
m
for f
a
m
|a
m−1
, l
m
for m = 0, 1...K.. Obtain the MLE ˆα
m
of the vector
parameter α
m
. For each time m, compute the weight
ˆ
W
g,
m
=
Q
m
k=0
f
g
(
A
k
|
¯
A
k−1
,
¯
L
k
)
f
k
(
A
k
|
¯
A
k−1
,
¯
L
k
;ˆα
k
)
2. Set
ˆ
T
K+1
= Y.
3. Recursively, for m = K, K − 1, ..., 0.
(a) Fit a generalized linear model b
m
¯
A
m
,
¯
L
m
; γ
m
, ς
m
= ϕ
h
γ
m
d
m
¯
A
m
,
¯
L
m
+ ς
m
ˆ
W
g,
m
i
, with ϕ
an inverse canonical link, for the conditional expectation E
h
ˆ
T
m+1
|
¯
A
m
,
¯
L
m
, C
g
m
= 0
i
by itera-
tively reweighted least squares (IRLS) among individuals with C
g
m
= 0; then (bγ
m
, bς
m
) satisfies
b
E
I (C
g
m
= 0)
d
m
(
¯
A
m
,
¯
L
m
)
ˆ
W
g,
m
ˆ
T
m+1
− b
m
¯
A
m
,
¯
L
m
; bγ
m
, bς
m
= 0
(b) set
ˆ
T
m
=
P
a
m
b
m
a
m
,
¯
A
m−1
,
¯
L
m
; bγ
m
, bς
m
f
g
a
m
|
¯
A
m−1
,
¯
L
m
4.
b
ψ
dr,plug
=
b
E
h
ˆ
T
0
i
As pointed out by Molina et al. (2017),
b
ψ
dr,plug
is K + 2 robust because, in addition to being doubly robust, it is also
(asymptotically) unbiased for ψ when, for any p ∈ {1, ..., K}, the models b
m
¯
A
m
,
¯
L
m
; γ
m
, ς
m
are correctly specified
for m ∈ {K, ..., p} and the models f
m
a
m
|a
m−1
, l
m
; α
m
are correctly specified for m ∈ {p − 1, ..., 0}.
When
ˆ
W
g,
m
is not used as a covariate, the above algorithm computes the iterative conditional expectation (ICE)
estimator of the g-formula for E[Y
g
] (Fine Point 21.2), which is a non-doubly robust estimator of the g-formula.
a single time point k = 0. The extension to time-varying treatments requires
that the model specifies as many equations as time points in the data. For
the time-varying treatment A = (A
0
, A
1
) at two time points in Table 21.1, we
specify a (saturated) additive structural nested mean model with two equations
For time k = 0: E
Y
a
0
,a
1
=0
− Y
a
0
=0,a
1
=0
|A
0
= a
0
= β
0
a
0
For time k = 1: E
Y
a
0
,a
1
− Y
a
0
,a
1
=0
|L
a
0
1
= l
1
, A
0
= a
0
, A
a
0
1
= a
1
=
= a
1
(β
11
+ β
12
l
1
+ β
13
a
0
+ β
14
a
0
l
1
)
By consistency, the conditional expectation for time k = 1 can be written
as E
Y
a
0
,a
1
− Y
a
0
,a
1
=0
|L
1
= l
1
, A
0
= a
0
, A
1
= a
1
. Since we assume sequen-
tial exchangeability for Y , we can and will replace (i) the conditional expec-
tation for k = 0 by E
Y
a
0
,a
1
=0
− Y
a
0
=0,a
1
=0
since A
0
= a
0
can be removed
from the conditioning event, and (ii) the conditional expectation for k = 1 by
E
Y
a
0
,a
1
− Y
a
0
,a
1
=0
|L
a
0
1
= l
1
, A
0
= a
0
since A
a
0
1
= a
1
can be removed from
the conditioning event.
21.4 G-estimation for time-varying treatments 285
Fine Point 21.2
Representations of the g-formula. The g-formula can be mathematically represented in several ways. These different
representations of the g-formula are nonparametrically equivalent but lead to different estimators in practice. Throughout
this book we have emphasized a representation of the g-formula that is the generalized version of standardization (in
the epidemiologic jargon). That is, the g-formula for a mean outcome is
P
l
E [Y |A = a, L = l] f (l) for a time-fixed
treatment and, as described in this chapter,
P
¯
l
E
Y |
¯
A = ¯a,
¯
L =
¯
l
K
Q
k=0
f
l
k
|¯a
k−1
,
¯
l
k−1
for a time-varying treatment.
Because a plug-in estimator based on this representation of the g-formula requires estimates of the joint density of the
confounders
K
Q
k=0
f
l
k
|¯a
k−1
,
¯
l
k−1
over time, we refer to it as a joint density modeling estimator of the g-formula.
An alternative representation of the g-formula is as iterated conditional expectations. For a time-fixed treatment, we
implicitly used this g-formula representation E [E [Y |A = a, L = l]] in Section 13.3. For a time-varying treatment, the
representation is an iterated conditional expectation (ICE) that can be recursively defined (Robins 1986). A plug-in
estimator based on the ICE representation of the g-formula requires the fitting of sequential predictive algorithms (e.g.,
regression models). The ICE estimator is described in Section 21.3 and Technical Point 21.4, where we combine it with
the estimation of IP weights to construct doubly (actually K + 2) robust estimators.
Another representation of the g-formula is IP weighting. In fact, as shown in Technical Point 2.3 for time-fixed
treatments, the standardized mean and the IP weighted mean are equal under positivity. The same is true for time-
varying treatments (Robins and Rotnitzky, 1992; Robins, 1993; Young et al., 2014). As described in this chapter, an
estimator based on the IP weighting representation of the g-formula requires the estimation of the conditional density of
treatment over time given past treatment and covariate history. We refer to these estimators as IP weighted estimators
rather than as g-formula estimators.
Hence the equation at time k = 1 models the effect of treatment at time
k = 1 within each of the 4 treatment and covariate histories defined by (A
0
, L
1
).
This component of the model is saturated because the 4 parameters β
1
in the
second equation parameterize the effect of a
1
on Y within the 4 possible levels
of past treatment and covariate history. The first equation models the effect
of treatment at time k = 0 when treatment at time k = 1 is set to zero. ThisEffect of a
1
is:
• β
11
in individuals with A
0
=
0, L
a
0
=0
1
= 0
• β
11
+ β
12
in those with A
0
=
0, L
a
0
=0
1
= 1
• β
11
+ β
13
in those with A
0
=
1, L
a
0
=1
1
= 0
• β
11
+β
12
+β
13
+β
14
in those
with A
0
= 1, L
a
0
=1
1
= 1
By consistency, L
a
0
1
= L
1
when
A
0
= a
0
.
component of the model is also saturated because it has one parameter β
0
to
estimate the effect within the only possible history (there is no prior treatment
or covariates, so everybody has the same history). The two equations of the
structural nested model are the reason why the model is referred to as nested.
The first equation models the effect of receiving treatment at time 0 and never
again after time 0, the second equation models the effect of receiving treatment
at time 1 and never again after time 1, and so on if we had more time points.
Let us use g-estimation to estimate the parameters of our structural nested
model with K = 1. We follow the same approach as in Chapter 14. We start
by considering the additive rank-preserving structural nested model for each
individual i
Y
a
0
,0
i
= Y
0,0
i
+ ψ
0
a
0
Y
a
0
,a
1
i
= Y
a
0
,0
i
+ ψ
11
a
1
+ ψ
12
a
1
L
a
0
1,i
+ ψ
13
a
1
a
0
+ ψ
14
a
1
a
0
L
a
0
1,i
,
where the second equation is restricted to individuals with A
0
= a
0
. That
is, the second equation is actually two equations, one for individuals with
A
0
= 1 and one for individuals with A
0
= 0. This allows us to replace, by
consistency, L
a
0
1,i
by L
1,i
, which will be needed for identification of the model
parameters from the observed data when, as in Figure 19.6, we do not have
sequential exchangeability for L
1
. We represent Y
a
0
=0,a
1
=0
i
by Y
0,0
i
to simplify
286 G-methods for time-varying treatments
the notation.
The first equation is a rank-preserving model because the effect ψ
0
is exactly
the same for every individual. Thus if Y
0,0
i
for subject i exceeds Y
0,0
j
for subject
j, the same ranking of i and j will hold for Y
1,0
—the model preserves ranks
across strategies. Also, under equation 2, if Y
1,0
i
for subject i exceeds Y
1,0
j
for
subject j, we can only be certain that Y
1,1
i
for individual i also exceeds Y
1,1
j
for individual j if both have the same values a
0
of A
0,i
and l
1
of L
1,i
= L
a
0
1,i
.
Because the preservation of the ranking is conditional on local factors (i.e.,
the value L
a
0
=1
1
), we refer to the second equation as a conditionally, or locally,
rank-preserving model.
As discussed in Chapter 14, rank preservation is biologically implausible
because of individual heterogeneity in unmeasured genetic and environmen-
tal risks. That is why our primary interest is in the structural nested mean
model, which is totally agnostic as to whether or not there is additional effect
heterogeneity across individuals due to unmeasured factors. However, givenThe proof can be found in Robins
(1994). Note that to fit an unsatu-
rated structural nested mean model
by g-estimation, positivity is not re-
quired.
sequential exchangeability for Y , a class of g-estimators (described below) of ψ
for the rank-preserving model are consistent for the parameters β of the mean
model, even if the rank-preserving model is misspecified.
The first step in g-estimation is linking the model to the observed data,
as we did in Chapter 14 for a time-fixed treatment. To do so, note that, by
consistency, the counterfactual outcome Y
a
0
,a
1
is equal to the observed out-
come Y for individuals who happen to be treated with treatment values a
0
and
a
1
. Formally, Y
a
0
,a
1
= Y
A
0
,A
1
= Y for individuals with (A
0
= a
0
, A
1
= a
1
).
Similarly Y
a
0
,0
= Y
A
0
,0
for individuals with (A
0
= a
0
, A
1
= 0), and L
a
0
1
= L
1
for individuals with A
0
= a
0
. Now we can rewrite the structural nested model
in terms of the observed data as
Y
A
0
,0
= Y − (ψ
11
A
1
+ ψ
12
A
1
L
1
+ ψ
13
A
1
A
0
+ ψ
14
A
1
A
0
L
1
)
Y
0,0
= Y
A
0
,0
− ψ
0
A
0
(we are omitting the individual index i to simplify the notation).
The second step in g-estimation is to use the observed data to compute
the candidate counterfactuals H
1
ψ
†
and H
0
ψ
†
. To do so, we use the
structural nested model with the true value ψ of the parameter replaced by
some value ψ
†
:
H
1
ψ
†
= Y −
ψ
†
11
A
1
+ ψ
†
12
A
1
L
1
+ ψ
†
13
A
1
A
0
+ ψ
†
14
A
1
A
0
L
1
H
0
ψ
†
= H
1
ψ
†
− ψ
†
0
A
0
As in Chapter 14, the goal is to find the value ψ
†
of the parameters that is equal
to the true value ψ. When ψ
†
= ψ and A
k−1
= a
k−1
, the candidate counter-
factual H
k
ψ
†
equals the true counterfactual Y
a
k−1
,0
k
under treatment a
k−1
through time k − 1 and treatment 0 afterwards. We can now use sequen-
tial exchangeability to conduct g-estimation at each time point. Fine Point
21.3 describes how to g-estimate the parameters ψ of our saturated structural
nested model. It turns out that all parameters of the structural nested model
are 0, which implies that all counterfactual means E [Y
g
] under any static or
dynamic strategy g are equal to 60. This result agrees with those obtained by
the g-formula and by IP weighting. G-estimation, like the g-formula and IP
weighting, succeeds where traditional methods failed.
In practice, however, we will encounter observational studies with multiple
times k and multiple covariates L
k
at each time. In general, a structural
21.4 G-estimation for time-varying treatments 287
Fine Point 21.3
G-estimation with a saturated structural nested model. Sequential exchangeability at k = 1 implies that, within
any of the four joint strata of (A
0
, L
1
), the mean of Y
A
0
,0
among individuals with A
1
= 1 is equal to the mean among
individuals with A
1
= 0. Therefore, the means of H
1
ψ
†
must also be equal when ψ
†
= ψ.
Consider first the stratum (A
0
, L
1
) = (0, 0). From data rows 1 and 2 in Table 21.2, we find that the mean of
H
1
(ψ) is 84 when A
1
= 0 and 84 − ψ
11
when A
1
= 1. Hence ψ
11
= 0. Next we equate the means of H
1
(ψ) in
data rows 3 and 4 corresponding to stratum (A
0
, L
1
) = (0, 1) to obtain 52 = 52 − ψ
11
− ψ
12
. Since ψ
11
= 0, we
conclude ψ
12
= 0. Continuing we equate the means of H
1
(ψ) in data rows 5 and 6 to obtain 76 = 76 − ψ
11
− ψ
13
.
Since ψ
11
= ψ
12
= 0, we conclude ψ
13
= 0. Finally, equating the means of H
1
(ψ) in data rows 7 and 8, we obtain
44 = 44 − ψ
11
− ψ
12
− ψ
13
− ψ
14
so ψ
14
= 0 as well.
To estimate ψ
0
, we first substitute the values ψ
11
, ψ
12
, ψ
13
, and ψ
14
into the expression for the mean of H
0
(ψ) in
Table 21.2. In this example, all parameters were equal to 0, so the mean of H
0
(ψ) was equal to the mean of the observed
outcome Y . We then use the first equation of the structural equation model to compute the mean of H
0
(ψ) for each
data row in the table by subtracting ψ
0
A
0
from the mean of H
1
(ψ), as shown in Table 21.3. Sequential exchangeability
Y
0,0
⊥⊥A
0
at time k = 0 implies that the means of H
0
(ψ) among the 16, 000 subjects with A
0
= 1 and the 16, 000
subjects with A
0
= 0 are identical. The mean of H
0
(ψ) is 84 × 0.25 + 52 ×0.75 = 60 among individuals with A
0
= 0,
(76 − ψ
0
) × 0.5 + (44 − ψ
0
) × 0.5 = 60 − ψ
0
among individuals with A
0
= 1. Hence ψ
0
= 0. We have completed
g-estimation.
nested mean model has as many equations as time points k = 0, 1...K. The
Table 21.2
A
0
L
1
A
1
Mean H
1
(ψ)
0 0 0 84
0 0 1 84 − ψ
1,1
0 1 0 52
0 1 1 52 − ψ
11
− ψ
12
1 0 0 76
1 0 1 76 − ψ
11
− ψ
13
1 1 0 44
1 1 1 44 − ψ
11
− ψ
12
−ψ
13
− ψ
14
Table 21.3
A
0
L
1
A
1
Mean H
0
(ψ)
0 0 0 84
0 0 1 84
0 1 0 52
0 1 1 52
1 0 0 76 − ψ
0
1 0 1 76 − ψ
0
1 1 0 44 − ψ
0
1 1 1 44 − ψ
0
most general form of structural nested mean models that we discuss in the
main text is the following (even more general structural nested mean models
are discussed in Technical Point 21.13). For each time k = 0, 1...K,
E
h
Y
a
k−1
,a
k
,0
k+1
− Y
a
k−1
,0
k
|L
a
k−1
k
= l
k
, A
k−1
= a
k−1
, A
k
= a
k
i
= a
k
γ
k
a
k−1
, l
k
, β
where
a
k−1
, a
k
, 0
k+1
is a static strategy that assigns treatment a
k−1
between
times 0 and k−1, treatment a
k
at time k, and treatment 0 from time k = 1 until
the end of follow-up K. The strategies
a
k−1
, a
k
, 0
k+1
and (a
k−1
, 0
k
) differ
only in that the former has treatment a
k
at k while the latter has treatment
0 at time k. Here each γ
k
a
k−1
, l
k
, ψ
†
is a known function of a parameter
vector ψ
†
such that γ
k
a
k−1
, l
k
, ψ
†
= 0
= 0 and β is the true value of ψ
†
.
Again, under sequential exchangeability for Y , we can drop A
k
= a
k
from
the above conditioning event. In our example with K = 1, γ
0
a
−1
, l
0
, β
is
just β
0
(l
0
and a
−1
can both be taken to be identically 0) and γ
1
a
0
, l
1
, β
is
β
11
+ β
12
l
1
+ β
13
a
0
+ β
14
a
0
l
1
.
Thus, a structural nested mean model is a model for the effect on the
mean of Y of a last blip of treatment of magnitude a
k
at k, as a function
γ
k
a
k−1
, l
k
, β
of past treatment and covariate history
a
k−1
, l
k
. See Tech-
nical Point 21.7 for the relationship between structural nested models and
marginal structural models.
We are now ready to discuss estimation of the parameters of a general
structural nested mean model with blip funcion γ
k
a
k−1
, l
k
, β
. To motivateThis blip function satisfies
γ
k
a
k−1
, l
k
, 0
= 0 so β = 0
under the null hypothesis of no
effect of treatment.
our estimation procedure, we will use the fact that a correctly specified locally
rank preserving model with true parameter ψ is also a correctly specified struc-
tural nested mean model with true parameter β = ψ (though the converse is
288 G-methods for time-varying treatments
Technical Point 21.7
Marginal structural models and structural nested models. A structural nested mean model is a semiparametric
marginal structural mean model if and only if, for all
a
k−1
, l
k
, β
,
γ
k
a
k−1
, l
k
, β
= γ
k
(a
k−1
, β)
does not depend on l
k
. Specifically, it is a semiparametric marginal structural mean model with the functional form
E
Y
a
= α
0
+
K
X
k=0
a
k
γ
k
(a
k−1
, β) ,
where a
0
= E
h
Y
0
K
i
is an unknown constant. However, such a structural nested mean model is not simply a marginal
structural mean model, because it also imposes the additional strong assumption that effect modification by past
covariate history is absent. In contrast, a marginal structural model is agnostic as to whether there is effect modification
by time-varying covariates.
If we specify a structural nested mean model γ
k
(a
k−1
, β), then we can estimate β either by g-estimation or IP
weighting. However the most efficient g-estimator will be more efficient than the most efficient IP weighted estimator
when the structural nested mean model (and thus the marginal structural mean model) is correctly specified, because
g-estimation uses the additional assumption of no effect modification by past covariates to increase efficiency.
In contrast, suppose the marginal structural mean model is correct but the structural nested mean model is incorrect
because γ
k
a
k−1
, l
k
, β
= γ
k
(a
k−1
, β). Then the g-estimates of β and E
Y
a
will be biased, while the IP weighted
estimates remain unbiased. Thus we have a classic variance-bias trade off. Given the marginal structural model,
g-estimation can increase efficiency if γ
k
a
k−1
, l
k
, β
= γ
k
(a
k−1
, β), but introduces bias otherwise.
not true). Given a structural nested mean model, we can define
H
k
ψ
†
= Y −
K
X
j=k
A
j
γ
j
A
j−1
, L
j
, ψ
†
A correctly specified locally rank preserving model with true parameter vector
ψ is equivalent to the statement that H
k
(ψ) is exactly equal to the counterfac-
tual Y
A
k−1
,0
k
in which the effects of the treatments from time j through K have
been removed. In particular, H
0
(ψ) is the value of Y
0
under no treatment.
However, if the assumption of local rank preservation is incorrect (as will
essentially always be the case if there is a treatment effect) but the struc-
tural nested mean model is correct, we still have that E
H
k
(β) |A
k
, L
k
equals
E
h
Y
A
k−1
,0
k
|A
k
, L
k
i
and that E [H
0
(β)] equals E
h
Y
0
i
. Thus, E
h
Y
0
i
can be
consistently estimated as the sample average of H
0
b
β
if we obtain a consis-
tent estimator of
b
β. This is what g-estimation provides.
With multiple time points or covariates, we will need to fit an unsaturated
structural nested mean model. For example, we might hypothesize that the
function γ
k
a
k−1
, l
k
, β
is the same for all k. The simplest model would be
γ
k
a
k−1
, l
k
, β
= β
1
, which assumes that the effect of a last blip of treatment
is the same for all past histories and all times k. Other options are β
1
+ β
2
k,
which assumes that the effect varies linearly with the time k of treatment, and
β
1
+ β
2
k + β
3
a
k−1
+ β
4
l
k
+ β
5
l
k
a
k−1
, which allows the effect of treatment at
k to be modified by the most recent treatment and covariate values.
21.4 G-estimation for time-varying treatments 289
To describe g-estimation for structural nested mean models with multiple
time points, suppose the nonsaturated model is γ
k
a
k−1
, l
k
, β
= β
1
. The
corresponding rank-preserving model entails H
k
ψ
†
= Y −
K
X
j=k
A
j
ψ
†
, which
can be computed from the observed data for any value ψ
†
. We will then
choose values ψ
low
and ψ
up
that are much smaller and larger, respectively, than
any substantively plausible value of ψ, and will compute (for each individual
and time) the value of H
k
ψ
†
for each ψ
†
on a grid from ψ
low
to ψ
up
, say
ψ
low
, ψ
low
+ 0.1, ψ
low
+ 0.2, ..., ψ
up
.
Then, for each value of ψ
†
, we will fit a pooled (over time) logistic regression
model
logit Pr
A
k
= 1|H
k
ψ
†
, L
k
, A
k−1
= α
0
+ α
1
H
k
ψ
†
+ α
2
W
k
for the probability of treatment at time k for k = 0, ..., K. Here W
k
=
w
k
L
k
, A
k−1
is a vector of covariates calculated from an individual’s covari-
ate and treatment data
L
k
, A
k−1
, α
2
is a row vector of unknown parameters,
and each person contributes K + 1 observations. The g-estimate of β is the
grid value of ψ
†
for which the estimate of α
1
is closest to 0. We can eliminateThe limits of the 95% confidence
interval for ψ are the limits of the
set of values ψ
†
that result in a P-
value > 0.05 when testing for α
1
=
0.
the need to search over the grid by defining the estimate
b
β to be the value of
ψ
†
such that the p-value of the score test of α
1
= 0 is equal to 1. That is
b
β is
the value of ψ
†
that solves
i=N,k=K
X
i=1,k=0
{A
i
− expit (bα
0
+ bα
2
W
i,k
)}H
i,k
ψ
†
= 0
where bα
0
and bα
2
are obtained by fitting the above logistic model with the
term α
1
set to 0. Standard equation solvers can be used. The estimator
b
β will
be consistent if (i) the structural nested mean model is correct, (ii) sequential
exchageability for Y holds, (iii) the model logit Pr
A
k
= 1|L
k
, A
k−1
= α
0
+
α
0
W
k
is correct, and (iv) H
k
ψ
†
enters the above logistic model linearly (i.e.,
as H
k
ψ
†
) rather than as
H
k
ψ
†
2
or any other non-linear function (see
Technical Point 14.2).
The procedure described above is the generalization to time-varying treat-
ments of the g-estimation procedure described in Chapter 14. For simplicity, we
considered a structural nested model with a single parameter β
1
, which implies
that the effect does not vary over time k or by treatment and covariate history.
Suppose now that the parameter β is a vector. To be concrete suppose we con-
sider the model with γ
k
a
k−1
, l
k
, β
= β
0
+ β
1
k + β
2
a
k−1
+ β
3
l
k
+ β
4
l
k
a
k−1
so
β is 5-dimensional and l
m
is 1-dimensional. Now to estimate 5 parameters one
requires 5 additional covariates in the treatment model. For example, we could
fit the model logit Pr
A
k
= 1|H
k
ψ
†
, L
k
, A
k−1
=
α
0
+ H
k
ψ
†
(α
1
+ α
2
k + α
3
A
k−1
+ α
4
L
k
+ α
5
L
k
A
k−1
) + α
6
W
k
The particular choice of covariates does not affect the consistency of the pointA 95% joint confidence interval for
β
j
are the set of values for which
the 5 degree-of-freedom score test
does not reject at the 5% level.
A less computationally demand-
ing approach is the univariate 95%
Wald confidence interval
b
β
j
± 1.96
times its standard error.
estimate of β, but it determines the width of its confidence interval.
The earlier g-estimation procedure then requires a search over a 5-dimensional
grid, one dimension for each component β
j
of β. So if we had 20 grid points for
each component we would have 20
5
different values of β on our 5 dimensional
grid. However, when the dimension of β is greater than 2, finding the g-estimate
b
β by a grid search may be computationally difficult. In that case we can elim-
inate the need to search over the grid by defining the g-estimate
b
β to be the
290 G-methods for time-varying treatments
Technical Point 21.8
A closed form estimator for linear structural nested mean models. When, as in all the examples we have discussed,
γ
k
A
k−1
, L
k
, β
= β
T
R
k
is linear in β with R
k
= r
k
¯
L
k
,
¯
A
k−1
being a vector of known functions, then, given the
model logit Pr
A
k
= 1|L
k
, A
k−1
= α
T
W
k
, there is an explicit closed form expression for
b
β given by
b
β =
i=N,k=K
X
i=1,k=0
A
i,k
X
i,k
(bα) Q
i,k
S
T
i,k
−1
i=N,k=K
X
i=1,k=0
Y
i
X
i,k
(bα) Q
i,k
with X
i,k
(bα) =
A
i,k
− expit
bα
T
W
i,k
, S
i,k
=
P
i=N,j=K
i=1,j=k
R
i,j
, and the choice of dimension-β functions Q
i,k
=
q
k
¯
L
i,k
,
¯
A
i,k−1
affects efficiency but not consistency. See Robins (1994) for the optimal choice of Q
k
.
In fact, when γ
k
a
k−1
, l
k
, β
is linear in β, we can obtain a closed-form 2
K+1
multiply robust estimator
e
β of β by
specifying a working model ς
T
D
k
= ς
T
d
k
¯
L
k
,
¯
A
k−1
for E
H
k
(β) |
¯
L
k
,
¯
A
k−1
= E
h
Y
A
k−1
,0
k
|
¯
L
k
,
¯
A
k−1
i
and defining
e
β
eς
=
i=N,k=K
X
i=1,k=0
A
i,k
X
i,k
(bα) Q
i,k
D
i,k
S
T
i,k
, D
T
i,k
−1
i=N,k=K
X
i=1,k=0
Y
i
X
i,k
(bα) Q
i,k
D
i,k
Specifically,
e
β will be a consistently asymptotically normal estimator of ψ if, for each k, either the model ς
T
D
k
for
E
h
Y
A
k−1
,0
k
|
¯
L
k
,
¯
A
k−1
i
is correct or the model for logit Pr
A
k
= 1|L
k
, A
k−1
is correct.
value of ψ
†
such that the p-value of the score test of α
1−5
= (α
1
, ..., α
5
)
T
= 0 is
equal to 1. That is
b
β is the value of ψ
†
that solves the 5 dimensional estimating
equation
i=N,k=K
X
i=1,k=0
A
i
− expit
bα
0
+ bα
T
6
W
i,k
H
i,k
ψ
†
(1, k, A
i,k−1
, L
i,k
, L
i,k
A
i,k−1
)
T
= 0
where bα
0
and bα
6
are obtained by fitting the above logistic model with α
1−5
set
to zero. Standard equation solvers can be used. Indeed, the solution
b
β to this
last equation exists in closed form when, as in all examples discussed in this
section, the structural nested mean model is linear in β. See Technical Point
21.8, which also describes a multiply robust form of the estimator.
Given a consistent g-estimator
b
β of the parameters of the structural nested
mean model, the last step is the estimation of the counterfactual mean E [Y
g
]
under the strategies g of interest. As discussed earlier, E
h
Y
0
i
can be con-
sistently estimated by the sample average
b
E
h
H
0
b
β
i
. If there is no effect
modification by past covariate history, i.e., γ
k
a
k−1
, l
k
, β
= γ
k
(a
k−1
, β) then
E
Y
a
under a static strategy a is estimated as
b
E
Y
a
=
b
E
h
Y
0
K
i
+
K
X
k=0
a
k
γ
k
a
k−1
,
e
β
On the other hand, if the structural nested mean model depends on L
k
or we
want to estimate E [Y
g
] under a dynamic strategy g, then we need to simulate
the L
k
using the algorithm described in Technical Point 21.9.
21.5 Censoring is a time-varying treatment 291
Technical Point 21.9
Estimation of E [Y
g
] after g-estimation of a structural nested mean model. Suppose the identifiability assumptions
hold, one has obtained a doubly robust g-estimate
e
β of a structural nested mean model γ
k
a
k−1
, l
k
, β
and one wishes
to estimate E [Y
g
] under a dynamic strategy g. To do so, one can use the following steps of a Monte Carlo algorithm:
1. Estimate the mean response E
h
Y
0
K
i
had treatment always been withheld by the sample average of H
0
e
β
over
the N study subjects. Call the estimate
b
E
h
Y
0
K
i
.
2. Fit a parametric model for f
l
k
|¯a
k−1
,
¯
l
k−1
to the data, pooled over persons and times, and let
b
f
l
k
|¯a
k−1
,
¯
l
k−1
denote the estimate of f
l
k
|¯a
k−1
,
¯
l
k−1
under the model.
3. Do for v = 1, ..., V ,
(a) Draw l
v,0
from
b
f (l
0
).
(b) Recursively for k = 1, ..., K draw l
v,k
from
b
f
l
k
|¯a
v,k−1
,
¯
l
v,k−1
with ¯a
v,k−1
= g
k−1
l
v,k−1
, the treatment
history corresponding to the strategy g.
(c) Let
b
∆
g,v
=
j=K
X
j=0
a
v,j
γ
j
a
v,j−1
, l
v,j
,
e
β
be the v
th
Monte Carlo estimate of Y
g
− Y
0
K
, where a
v,j
=
g
j
l
v,j−1
.
4. Let
b
E [Y
g
] =
b
E
h
Y
0
K
i
+
v=V
X
v=1
b
∆
g,v
/V be the estimate of
b
E [Y
g
] .
If the model for f
l
k
|¯a
k−1
,
¯
l
k−1
, the structural nested mean model γ
k
a
k−1
, l
k
, β
, and either the treatment model
Pr
A
k
= 1|L
k
, A
k−1
or the outcome model E
h
Y
A
k−1
,0
k
|
¯
L
k
,
¯
A
k−1
i
are correctly specified, then
b
E [Y
g
] is consistent
for E [Y
g
]. Confidence intervals can be obtained using the nonparametric bootstrap.
Note that γ
k
a
k−1
, l
k
,
e
β
will converge to 0 if the estimate
e
β is consistent for β = 0. Thus
b
∆
g,v
will converge to zero
and
b
E [Y
g
] to
b
E
h
Y
0
K
i
even if the model for f
l
k
|¯a
k−1
,
¯
l
k−1
is incorrect. That is, the structural nested mean model
preserves the null if the identifiability conditions hold and we either know (as in a sequentially randomized experiment)
Pr
A
k
= 1|L
k
, A
k−1
or have a correct model for either Pr
A
k
= 1|L
k
, A
k−1
or E
h
Y
A
k−1
,0
k
|
¯
L
k
,
¯
A
k−1
i
for each k.
21.5 Censoring is a time-varying treatment
Throughout this chapter we have used an example in which there is no cen-You may want to re-read Section
12.6 for a refresher on censoring. soring: the outcomes of all individuals in Table 21.1 are known. In practice,
however, we will often encounter situations in which some individuals are lost to
follow-up and therefore their outcome values are unknown or (right-)censored.
We have discussed censoring and methods to handle it in Part II of the book.
In Chapter 8, we showed that censoring may introduce selection bias, even
under the null. In Chapter 12, we discussed how we are generally interested in
the causal effect if nobody in the study population had been censored.
However, in Part II we only considered a greatly simplified version of cen-
soring under which we did not specify when individuals were censored during
the follow-up. That is, we considered censoring C as a time-fixed variable. A
more realistic view of censoring is as a time-varying variable C
1
, C
2
, ...C
K+1
,
292 G-methods for time-varying treatments
where C
m
is an indicator that takes value 0 if the individual remains uncen-Conditioning on being uncensored
(C = 0) induces selection bias un-
der the null when C is either a col-
lider on a pathway between treat-
ment A and the outcome Y , or the
descendant of one such collider.
sored at time m and takes value 1 otherwise. Censoring is a monotonic type of
missing data, i.e., if an individual’s C
m
= 0 then all previous censoring indi-
cators are also zero (C
1
= 0, C
2
= 0....C
m−1
= 0). Also, by definition, C
0
= 0
for all individuals in a study; otherwise they would have not been included in
the study.
If an individual is censored at time m, i.e., when C
m
= 1, then treatments,
confounders, and outcomes measured after time m are unobserved. Therefore,
the analysis becomes necessarily restricted to uncensored person-times, i.e.,
those with C
m
= 0. For example, the g-formula for the counterfactual mean
outcome E [Y
¯a
] from section 21.1 needs to be rewritten as
X
¯
l
E
Y |
¯
C =
¯
0,
¯
A = ¯a,
¯
L =
¯
l
K
Y
k=0
f
l
k
|c
k
= 0, ¯a
k−1
,
¯
l
k−1
,
with all the terms being conditional on remaining uncensored.
Suppose the identifiability conditions hold with treatment A
m
replaced by
(A
m
, C
m+1
) at all times m. Then it is easy to show that the above expression
corresponds to the g-formula for the counterfactual mean outcome E
Y
¯a,¯c=
¯
0
under the joint treatment (¯a, ¯c =
¯
0), i.e., the mean outcome that would haveThe use of the superscript ¯c =
¯
0
makes it explicit the causal contrast
that many have in mind when they
refer to the causal effect of treat-
ment
¯
A, even if they choose not to
use the superscript ¯c =
¯
0.
been observed if all individuals have received treatment strategy ¯a and no
individual had been lost to follow-up.
The counterfactual mean E
Y
¯a,¯c=
¯
0
can also be estimated via IP weighting
of a structural mean model when the identifiability conditions hold for the
joint treatment
¯
A,
¯
C
. To estimate this mean, we might fit, e.g., the outcome
regression model
E
Y |A,
¯
C =
¯
0
= θ
0
+ θ
1
cum
A
to the pseudo-population created by the nonstabilized IP weights W
¯
A
× W
¯
C
where
W
¯
C
=
K+1
Y
k=1
1
Pr
C
k
= 0|C
k−1
= 0,
¯
A
k−1
,
¯
L
k−1
We estimate the denominator of the weights by fitting a logistic regression
model for Pr
C
k
= 0|C
k−1
= 0,
¯
A
k−1
,
¯
L
k−1
. Technical Point 21.10 shows the
extension to survival analysis with a failure time outcome.
In the pseudo-population created by the nonstabilized IP weights, the
censored individuals are replaced by copies of uncensored individuals with
the same values of treatment and covariate history. Therefore the pseudo-
population has the same size as the original study population before censoring,
that is, before any losses to follow-up occur. The nonstabilized IP weights
abolish censoring in the pseudo-population.
Or we can use the pseudo-population created by the stabilized IP weights
SW
¯
A
× SW
¯
C
, whereRemember:
The estimated IP weights SW
¯
C
have mean 1 when the model for
Pr
C
k
= 0|
¯
A
k−1
, C
k−1
= 0,
¯
L
k
is correctly specified.
SW
¯
C
=
K+1
Y
k=1
Pr
C
k
= 0|C
k−1
= 0,
¯
A
k−1
Pr
C
k
= 0|C
k−1
= 0,
¯
A
k−1
,
¯
L
k−1
We estimate the denominator and numerator of the IP weights via two separate
models for Pr
C
k
= 0|C
k−1
= 0,
¯
A
k−1
,
¯
L
k−1
and Pr
C
k
= 0|C
k−1
= 0,
¯
A
k−1
,
respectively.
The pseudo-population created by the stabilized IP weights is of the same
size as the original study population after censoring, i.e., the proportion of
21.5 Censoring is a time-varying treatment 293
Technical Point 21.10
Survival analysis with time-varying treatments. Chapter 17 describes g-methods to estimate the effect of point
interventions on failure time outcomes. This chapter describes g-methods to estimate the effect of sustained strategies
on non-failure time outcomes. In practice, we often use g-methods to estimate the effect of sustained strategies on
failure time outcomes by combining the methods described in Chapter 17 with those in this chapter. Below we sketch
two approaches, based on the g-formula and on IP weighting, to estimate the counterfactual risk Pr
h
D
¯a,¯c=
¯
0
k+1
= 1
i
under
treatment strategy ¯a if sequential exchangeability, positivity, and consistency hold. The causal diagram in Figure 21.4
depicts such setting with two time points and the failure time outcome represented by time-varying indicators as in
Chapter 17. From each indicator D
k
there should be arrows into all future variables on the graph, but we omitted these
arrows to reduce clutter. For simplicity, we also omitted the time-varying indicators for censoring.
The risk Pr
h
D
¯a,¯c=
¯
0
k+1
= 1
i
is identified by 1 minus the g-formula for Pr
h
D
¯a,¯c=
¯
0
k+1
= 0
i
:
X
¯
l
k
Pr
D
k+1
= 0|
¯
A
k
= ¯a
k
,
¯
L
k
=
¯
l
k
, D
k
= C
k+1
= 0
×
k
Y
m=0
f
l
m
|¯a
m−1
,
¯
l
m−1
, D
m
= C
m
= 0
Pr
D
m
= 0|
¯
A
m−1
= ¯a
m−1
,
¯
L
m−1
=
¯
l
m−1
, D
m−1
= C
m
= 0
.
A plug-in g-formula estimate can then be obtained by fitting models for the discrete-time hazards
Pr
D
k+1
= 1|
¯
A
k
= ¯a
k
,
¯
L
k
=
¯
l
k
, D
k
= C
k+1
= 0
and for the conditional density f
l
k
|¯a
k−1
,
¯
l
k−1
, D
k
= C
k
= 0
of
the confounders L over time. As described in Chapter 17, a pooled logistic model can be used to approximate the
hazards. See Young et al. (2011) for details and an application. Wen et al. (2021) describe ICE g-formula estimators.
An alternative is to fit a pooled logistic model for the hazards Pr
D
k+1
= 1|
¯
A
k
= ¯a
k
,
¯
L
k
=
¯
l
k
, D
k
= C
k+1
= 0
in
which each individual at time k receives the time-varying nonstabilized IP weight W
¯
A
k
× W
¯
C
k
, where
W
¯
A
k
=
k
Y
m=0
1
f
A
m
|
¯
A
m−1
, D
m
= C
m
= 0,
¯
L
m
, W
¯
C
k
=
k
Y
m=1
1
Pr
C
m
= 0|
¯
A
m−1
, D
m−1
= C
m−1
= 0,
¯
L
m−1
,
or its corresponding stabilized IP weight at each time k. The parameters of that model estimate the parameters
of a marginal structural pooled logistic model for Pr
h
D
¯a,¯c=
¯
0
k+1
= 1|D
¯a,¯c=
¯
0
k
= 0
i
(Robins 1998a). For details and an
application, see Hern´an et al. (2001). Wen et al. (2022) review multiply robust estimators for survival analysis with
time-varying treatments.
censored individuals in the pseudo-population is identical to that in the study
population at each time k. The stabilized weights do not eliminate censor-
Figure 21.4
ing in the pseudo-population, they make censoring occur at random at each
time k with respect to the measured covariate history
¯
L
k
. That is, there is
selection but no selection bias. Regardless of the type of IP weights used, in
the pseudo-population there are no arrows from L
k
and A
k
into future C
m
for
m > k. Importantly, under the exchangeability conditions for the joint treat-
ment
¯
A,
¯
C
, IP weighting can unbiasedly estimate the joint effect of
¯
A,
¯
C
even when some components of
¯
L are affected by prior treatment.
Finally, when using g-estimation of structural nested models, we first need
to adjust for selection bias due to censoring by IP weighting. In practice,
this means that we first estimate nonstabilized IP weights W
¯
C
for censoring
to create a pseudo-population in which nobody is censored, and then apply
g-estimation to the pseudo-population.
294 G-methods for time-varying treatments
21.6 The big g-formula
This chapter and the previous two chapters privilege methods that rely on se-
quential exchangeability given the measured covariates L and identification by
the g-formula. The reason is that, in practice, few causal analyses of complex
longitudinal data have relied on other identifying conditions and formulas. For
example, there are few realistic applications based on the identifying condi-
tions under which the front door formula is the identifying formula. However,
regardless of substantive plausibility and practical applications, different iden-
tifying conditions and their formulas are mathematically linked to sequential
exchangeability and the g-formula based on all variables—both measured and
unmeasured—as we now explain.
When sequential exchangeability holds given the measured covariates L, we
have discussed how the g-formula based on the measured time-varying covari-
ates L identifies causal effects of a time-varying treatment A on an outcome Y .
Now suppose we have a causal DAG with both observed variables
A, L, Y
and unobserved variables U, and that the measured variables L are insufficient
to achieve sequential exchangeability.
For any causal DAG, the combination of measured and unmeasured vari-
ables X = (L, U ) ensures (joint) sequential exchangeability as any parent of a
treatment variable is contained in either A or X. Therefore, if every variable
on a causal diagram were measured and positivity held, the g-formula based on
X would identify the counterfactual mean E [Y
g
] under any treatment strategy
g. We refer to the g-formula with L replaced by X as the big g-formula because
it is not based solely on the observed data.
Given a causal DAG, treatment A and outcome Y , a treatment strategy
g, and factuals
A, L, Y, U
, we can explicitly write down the big g-formulaWe refer to
A, L, Y, U
as factu-
als to distinguish them from coun-
terfactuals. Factuals are variables
that exist in the actual world. In
contrast to the observed variables,
some factuals, such as U, are not
available for data analysis, often be-
cause they were not measured.
for the distribution (density) of Y
g
. The big g-formula depends only on the
distribution of the factuals
A, L, Y, U
.
The big g-formula is the right formula to identify the counterfactual density
under any treatment strategy, but the big g-formula cannot be used in practice
because it includes unmeasured variables. An interesting math question is then:
can the big g-formula be reduced to a functional of the joint distribution of
the observed data
A, L, Y
? If it can, then we will have a new formula that
is not expressed as a g-formula but that (i) reproduces the results of the big
g-formula (and therefore is a correct formula) and (ii) is written in terms of
the distribution of the observed variables only (and therefore is a formula that
can be used in data analyses).
For example, under the identifying conditions referred to as the front door
criterion, the big g-formula for E[Y
a
] reduces to a formula that only includes
observed variables—the front door formula (see the proof in Technical Point
21.11). Therefore, the front door formula is a valid formula for the mean of
E [Y
a
] under the front door assumptions embedded in the causal diagram of
Figure 7.14.
More generally, we would like to be able to answer the following two ques-
tions. First, can we always determine whether the big g-formula can be rewrit-These questions were completely
settled by the work of Tian and
Pearl (2002), Shpitser and Pearl
(2006), and Huang and Valtorta
(2006).
ten as a formula that depends only on the distribution of the observed variables
A, L, Y
, while making no assumptions other than the joint distribution of
A, L, Y, U
obeys the d-separation relations implied by the causal DAG? Sec-
ond, when the answer to the previous question is yes, can we explicitly display
such an identifying formula? Both of these questions have been answered in
the affirmative.
Importantly, these are purely mathematical questions about properties of
21.6 The big g-formula 295
Technical Point 21.11
A big g-formula proof of the front door formula. In Technical Point 7.4, we provided a proof of the front door
formula for the counterfactual probability Pr [Y
a
= y] under the causal diagram of Figure 7.14. Here we provide another
proof using the big g-formula. This second proof relies on the conditional independencies implied by Figure 7.14, but it
does not require that the counterfactuals Y
m
exist.
The big g-formula for Pr [Y
a
= y] under Figure 7.14 is
X
m
X
u
Pr[Y = y|M = m, A = a, U = u] Pr[M = m|A = a, U = u] Pr[U = u].
Since data on U are not available, Pr [Y
a
= y] is identified if and only if the big g-formula depends exclusively on the
distribution of the observed data (Y, M, A). We now show that is indeed the case because, under the above assumptions,
the g-formula reduces to the front door formula.
Using d-separation, we can rewrite the big g-formula as
P
m
Pr[M = m|A = a]
P
u
Pr[Y = y|M = m, U = u] {
P
a
′
Pr[U = u|A = a
′
] Pr[A = a
′
]}
by U⊥⊥M|A and A⊥⊥Y |M, U
=
P
m
Pr[M = m|A = a]
P
a
′
{
P
u
Pr[Y = y|M = m, A = a
′
, U = u] Pr[U = u|M = m, A = a
′
]}Pr[A = a
′
]
by U⊥⊥M|A and A⊥⊥Y |M, U
=
P
m
Pr[M = m|A = a]
P
a
′
Pr[Y = y|M = m, A = a
′
] Pr[A = a
′
], which is the front door formula.
We now provide yet another proof of the front door formula that also does not require that the counterfactuals Y
m
exist. After establishing that Pr [Y
a
= y] is a function of the distribution of (Y, M, A, U) given by the big g-formula, we
can apply a coupling argument. Suppose all agree on substantive grounds that a well-defined Y
m
does not exist. Yet
any factual data distribution that is Markov with respect to Figure 7.14 is compatible with an underlying FFRCISTG
model “as detailed as the data”(Robins and Richardson, 2010) which, by definition, formally includes a variable Y
m
.
The proof in Technical Point 7.4 demonstrated that, under this model, the big g-formula equals the front door formula.
It follows that there cannot exist a factual distribution Markov with respect to Figure 7.14 where this equality fails; for
if it failed, that factual distribution would not be compatible with an FFRCISTG model “as detailed as the data”.
Technical Point 21.12 presents an alternative proof of the front door formula based on a SWIG property.
distributions over
A, L, Y, U
known to obey certain independence relations
characterized by d-separation on the DAG. That is, these questions make no
reference to either counterfactuals or to causality. The only connection to
causality is the claim that the DAG is a causal DAG. If so, the big g-formula
will have a causal interpretation. If not, the affirmative answers, though still
true, will have no causal meaning. Of course, in observational analyses, we
can never know with certainty that a graph that we conjecture to be a causal
diagram is indeed a causal diagram.
296 G-methods for time-varying treatments
Technical Point 21.12
A front door formula proof using d-separation of treatment nodes on SWIGs. Here we provide another proof of
the front door formula using an important property of SWIGs that we have yet to discuss.
Given a causal diagram G, let G
a
be the associated SWIG for strategy a, and B
a
and C
a
two disjoint subsets of
the observed non-treatment nodes
Y
a
, L
a
. We assume only treatment counterfactuals are well-defined. The SWIG
G
a
satisfies the following property (Shpitser et al., 2022): If the fixed node a
m
is d-separated from B
a
conditional on
C
a
, then Pr
B
a
= b|C
a
= c
does not depend on a
m
. This property does not conflict with the previously discussed
fact that any path that contains a treatment a
m
as a non-endpoint is blocked. To make clear what the new property
means, consider the SWIG G
a
implied by the front door diagram in Figure 7.14. On SWIG G
a
, define B
a
= Y
a
and
C
a
=
M
a
′
, A
. Then a is d-separated from B
a
given C
a
as the only path from a to Y
a
goes through the non-collider
M
a
′
in C
a
. Thus, according to our property E [Y
a
|M
a
, A] = E
h
Y
a
′
|M
a
′
, A
i
for any a and a
′
. Note the property is
not cross-world; rather, it specifies a relationship between different single-world counterfactual distributions.
We now use this SWIG property to prove the front door formula when well-defined counterfactuals Y
m
do not exist.
We continue to assume that (Y
a
, M
a
, A) factor according to the SWIG G
a
and
Y
a
′
, M
a
′
, A
factor according to the
SWIG G
a
′
. We follow the proof in Technical Point 7.4 until we come to the point where we must prove
E [Y
a
|M
a
] =
X
a
′
E [Y |M, A = a
′
] Pr (A = a
′
) .
We now have E [Y
a
|M
a
] =
P
a
′
E [Y
a
|M
a
, A = a
′
] Pr (A = a
′
|M
a
) =
P
a
′
E [Y
a
|M
a
, A = a
′
] Pr (A = a
′
) by M(a) d-
separated from A. Our new SWIG property implies that E [Y
a
|M
a
, A = a
′
] = E
h
Y
a
′
|M
a
′
, A = a
′
i
= E [Y |M, A = a
′
]
where the last equality is by consistency. Thus, E [Y
a
|M
a
] =
P
a
′
E [Y |M, A = a
′
] Pr (A = a
′
) as required. Interest-
ingly, it follows that, although E [Y
a
|M
a
] = E
h
Y
a
′
|M
a
′
i
for all a, a
′
, nonetheless E [Y
a
|M
a
] = E [Y |M ] because
E [Y |M ] =
P
a
′
E [Y |M, A = a
′
] Pr (A = a
′
|M) and, unlike the counterfactual M
a
, the observed factual M = M
A
is
not independent of A.
21.6 The big g-formula 297
Technical Point 21.13
Formal definition of a general structural nested mean model. Robins (2004) noted there is nothing special about
¯
0 as the strategy that is followed after a final blip of treatment in a structural nested mean model (SNMM). We can
instead define the blip functions relative to an arbitrary strategy g as follows. Given g = (g
0
, g
1
, ..., g
K
), an additive
SNMM is a model for the causal effect on Y (conditional on treatment and covariate history through time t) of a blip
a
t
of treatment at t and then following g from time t + 1 onward versus following g from time t onward. That is, an
additive SNMM models the counterfactual contrast
γ
g
t
a
t,
l
t
= E[Y
a
t−1
,a
t
,g
t+1
− Y
a
t−1
,g
t
,g
t+1
|A
t−1
= a
t−1
, A
t
= a
t
, L
t
= l
t
]
for t = 0, ..., K with a = (a
0
, a
1
, ..., a
K
) , g
t+1
= (g
t+1
, ..., g
K
). We write γ
g
t
a
t,
l
t
as γ
g
t
a
t−1,
a
t
, l
t
and Y
a
t−1
,g
t
as Y
a
t−1
,g
t
,g
t+1
when we want to emphasize the unique role of a
t
and g
t
. Note that γ
g
t
a
t−1,
a
t
, l
t
≡ 0 when a
t
=
g
t
a
t−1,
l
t
. If, as in the main text, we assume sequential exchangeability, then A
t
= a
t
can be dropped from the
conditioning event in the definition of γ
g
t
a
t,
l
t
.
An SNMM assumes γ
g
t
a
t,
l
t
= γ
g
t
a
t,
l
t
; β
where γ
g
t
a
t,
l
t
; β
†
is a known function taking the value 0 if the
finite-dimensional parameter vector β
†
equals 0 or a
t
= g
t
a
t−1,
l
t
. If we define
H
k
(γ
g
) = Y −
K
X
t=k
γ
g
t
A
t,
L
t
,
it follows from consistency alone (Robins 2004) that E[H
k
(γ
g
) |L
k
, A
k
] = E[Y
A
k−1
,g
k
|L
k
, A
k
] for k = 0, ..., K and
E[H
0
(γ
g
)] = E[Y
g
]. Therefore, if we can identify the γ
g
t
a
t,
l
t
, we can identify E[Y
A
k−1
,g
k
|L
k
, A
k
] and E[Y
g
]. Under
positivity and sequential exchangeability, the last set-off equation implies E[H
k
(γ
g
) |L
k
, A
k
] = E[H
k
(γ
g
) |L
k
, A
k−1
]
which implies the γ
g
t
a
t,
l
t
are nonparametrically identified. Robins (2004) also defined an optimal regime structural
nested model (opt-SNMM) and showed how, under positivity and sequential exchangeability, one can use the opt-SNMM
to estimate the optimal treatment strategy g
opt
= arg max
g
[E (Y
g
)].
But sequential exchangeability is not the only possible identifying assumption. For example, Zahn et al. (2022)
showed that the γ
g
t
a
t,
l
t
are identified under a time-varying parallel trends assumption that generalizes the identifying
assumption typically made for difference-in-differences estimation with time-varying treatments and covariates.
In Technical Point 21.9, we took g in the SNMM to be the strategy “never treat”, i.e., g = 0, and we described an
algorithm to identify E[Y
g
] for every strategy g under the assumption of sequential exchangeability. When sequential
exchangeability does not hold, we can use other assumptions (e.g., time-varying parallel trends) that suffice to identify
E[Y
g
] for the g used to define the SNMM, but not to identify E[Y
g
′
] for any other strategy g
′
. To do so, we need
additional assumptions. For example Shahn et al. (2022) showed that if, in addition to assuming time-varying parallel
trends, one assumes that, conditional on past treatment and measured covariate history, there is no additive effect
modification by unmeasured confounders U, then E[Y
g
′
] is identified for all g
′
. This implies that the optimal strategy
g
opt
= argmax
g
′
E[Y
g
′
] is identified. Shahn et al. (2022) show how one can use structural nested mean models to
estimate g
opt
.
298 G-methods for time-varying treatments
Chapter 22
TARGET TRIAL EMULATION
As discussed in Part I, causal inference from observational data can be viewed as an attempt to emulate a hypo-
thetical randomized trial, which we refer to as the target trial. However, Parts I and II only referred to simplistic
target trials that compared time-fixed treatments. Since we now have all the tools that are needed to tackle causal
inferences with time-varying treatments, we are now ready to discuss realistic target trials that compare sustained
treatment strategies. This chapter generalizes the concept of the target trial to sustained treatment strategies
and outlines a unified framework for causal inference, regardless of whether the data arose from a randomized
experiment or an observational study.
This chapter also describes a taxonomy of causal effects that may be of interest when emulating a target
trial, including observational analogs of intention-to-treat and per-protocol effects. Valid estimation of those
causal effects generally requires data on time-varying prognostic factors and treatments, as well as appropriate
adjustment for those time-varying factors using g-methods. It is precisely the development of g-methods that
makes the concepts discussed here something more than a formal exercise: if data are available on all important
fixed and time-varying confounders, the effects of interest can now be validly estimated.
22.1 Intention-to-treat effect and per-protocol effect
Consider a randomized trial in which individuals at risk of being infected by
a dangerous virus are randomly assigned to a joint treatment of immediate
vaccination plus an experimental antiviral therapy in case of being infected
(Z = 1) or to standard of care (Z = 0), which includes no vaccination and
no antiviral therapy. Figure 22.1 represents this trial with assigned treatment
Z, received treatment A, and outcome (death) Y . For a given individual,
Figure 22.1
the value of Z and A may differ because of lack of adherence to the assigned
treatment some individuals assigned to vaccine (Z = 1) may not receive it
(A = 0) because they refuse to be vaccinated, some individuals assigned to no
vaccine (Z = 0) may still obtain a vaccine (A = 1) outside of the study. The
variable U represents the unmeasured risk factors that influence an individual’s
decision to get vaccinated.
As shown in Figure 22.1, the assigned treatment Z can have a causal effect
on the outcome Y through two different pathways. First, treatment assignment
Z may affect the outcome Y simply because it affects the received treatment
A. Individuals assigned to vaccine are more likely to receive a vaccine, as
represented by the arrow from Z to A. If receiving a vaccine has a causal
effect on mortality, as represented by the arrow from A to Y , then assignment to
vaccine has a causal effect on the outcome Y through the pathway Z → A → Y .
Second, treatment assignment Z may affect the outcome Y through path-
ways that are not mediated by received treatment A. For example, awareness
of the assigned treatment might lead to changes in the participants’ behavior
individuals aware of having been assigned to vaccination plus a promising an-
tiviral therapy may become less careful about being infected. These behavioral
changes are represented by the direct arrow from Z to Y .
300 Target trial emulation
Fine Point 22.1
The exclusion restriction (again). The existence of the arrow Z → Y in Figure 22.1 represents a direct effect of
assignment on the outcome not through treatment. When this arrow exists, we say that the exclusion restriction does
not hold. See Technical Point 16.1 for a formal discussion of the exclusion restriction.
Often investigators try to partly “de-contaminate” the effect of Z by eliminating the arrow Z → Y as shown in
Figure 22.2 (same as Figure 16.1), which depicts the exclusion restriction of no direct arrow from Z to Y . To do so,
they withhold knowledge of the assigned treatment Z from participants and their doctors. For example, investigators
would administer the vaccine to those randomly assigned to Z = 1, and a placebo (an identical injection except that it
does not contain vaccine) to those assigned to Z = 0. Because participants and their doctors do not know whether the
injection they are given is the active treatment or a placebo, they are said to be “blinded” and the study is referred to as a
double-blind placebo-controlled randomized trial. In Chapter 16, we used the concept of double-blind placebo-controlled
randomized trial to motivate the concept of instrumental variable.
A double-blind treatment assignment is often unfeasible. Many studies cannot be effectively blinded because there is
no practical way of administering a convincing placebo (e.g., for open heart surgery), because side effects of a treatment
will make apparent who is taking it, etc. Also, blinding (and placebo control) is not advised when investigators are
interested in quantifying the treatment effect in the real world, in which no blinding (or placebo) exists.
Hence, the causal effect of the assigned treatment Z depends not only on
the strength of the arrow A −→ Y (the effect of the received treatment), but
Figure 22.2
also on the strength of the arrows Z −→ A (the degree of adherence to the
assigned treatment in the study) and Z −→ Y (the concurrent behavioral
changes). The effect of Z is not “the effect of treating with A” but rather
“the effect of assigning participants to being treated with A” or “the effect of
having the intention of treating with A,” which is why the effect of randomized
assignment Z is often referred to as the intention-to-treat effect.
No confounding is expected for the effect of assigned treatment because Z is
randomly assigned. Exchangeability Y
z
⊥⊥Z is expected to hold for the assigned
treatment Z because there are no backdoor paths from Z to Y in Figure 22.1.
Association between Z and Y implies a causal effect of Z on Y , whether or not
all individuals adhered to the assigned treatment. The associational risk ratio
Pr[Y = 1|Z = 1]/ Pr[Y = 1|Z = 0] equals the causal intention-to-treat risk
ratio Pr[Y
z=1
= 1]/ Pr[Y
z=0
= 1]. The analysis that estimates the unadjusted
association between Z and Y to estimate the intention-to-treat effect is referred
to as an intention-to-treat analysis. See Fine Point 22.2 for common variations
of the intention-to-treat analysis that are generally biased.
Now consider the causal effect of treatment that would have been observed
if all individuals had adhered to their assigned treatment as specified in the pro-
tocol of the experiment, which we refer to as the per-protocol effect. Through-The per-protocol effect is defined
by the contrast Pr[Y
z=1,a=1
= 1]
vs. Pr[Y
z=0,a=0
= 1] or, under the
exclusion restriction, by the con-
trast Pr[Y
a=1
= 1] vs. Pr[Y
a=0
=
1]. In the text we use the latter for
notational simplicity.
out most of this book, we have assumed perfect adherence to the assigned
treatment so that the values of assigned treatment Z and received treatment
A coincide for all participants. that is, we assumed that U does not exist and
thus the treated (A = 1) and the untreated (A = 0) are exchangeable, Y
a
⊥⊥A.
Consider now a setting in which U represents high risk of infection (1: yes,
0: no) and in which individuals at high risk of infection (U = 1) in the Z = 0
group tend to seek vaccination (A = 1) outside of the study. If that occurs,
then the group A = 1 would include a higher proportion of high-risk individuals
than the group A = 0: the groups A = 1 and A = 0 would not be exchangeable,
and thus the associational risk ratio Pr[Y = 1|A = 1]/ Pr[Y = 1|A = 0] would
not equal the (causal) per-protocol risk ratio Pr[Y
a=1
= 1]/ Pr[Y
a=0
= 1]. As
22.1 Intention-to-treat effect and per-protocol effect 301
Fine Point 22.2
Pseudo-intention-to-treat analysis and modified intention-to-treat analysis. An intention-to-treat analysis is
unbiased for the intention-to-treat effect because it includes all randomized individuals. Therefore, variations of the
intention-to-treat analysis that only include a subset of the randomized individuals may be biased.
When some individuals do not complete the follow-up, their outcomes are unknown and thus the analysis needs to
be restricted to individuals with complete follow-up. Thus, we can only conduct a pseudo-intention-to-treat analysis
Pr[Y = 1|Z = 1, C = 0]/ Pr[Y = 1|Z = 0, C = 0] where C = 0 indicates that an individual remained uncensored until
the measurement of Y . As described in Chapter 8, censoring may induce selection bias and thus the pseudo-intention-
to-treat estimate may be a biased estimate, in either direction, of the intention-to-treat effect. In the presence of loss
to follow-up or other forms of censoring, the intention-to-treat analysis of randomized experiments requires appropriate
adjustment for selection bias. See Section 21.5 and Little et al. (2012) for additional discussion.
For sustained treatment strategies, a common approach is to restrict the intention-to-treat analysis to individuals who
at least initiated their assigned strategy (e.g., took at least one pill). This approach, known as a modified intention-to-
treat analysis, includes only a subset of randomized individuals and may therefore be biased for the intention-to-treat
effect. A modified intention-to-treat analysis generally requires adjustment for the risk factors that affect adherence.
indicated by the backdoor path A ← U → Y , there is confounding for the
effect of A on Y and estimating the per-protocol effect requires adjustment.
That is, estimation of the per-protocol effect requires viewing the randomized
experiment as an observational study. Fine Point 22.3 describes conventional
approaches to quantify the per-protocol effect that missed this point.
The lack of confounding largely explains why the intention-to-treat effect is
privileged in many randomized experiments: “the effect of having the intention
of treating with A” may not be the effect that we want—“the effect of treating
with A” or the per-protocol effect—but it is easier to compute. As often occurs
when a less interesting quantity is easier to compute than a more interesting
quantity, we tend to come up with arguments to justify the use of the less
interesting quantity. The intention-to-treat effect is no exception. We now
discuss why several well-known justifications for the intention-to-treat effect
need to be taken with a grain of salt.
A common justification for the intention-to-treat effect is that it preserves
the null. That is, if treatment A has a null effect on Y , then assigned treatment
Z will also have a null effect on Y . Null preservation is a key property because
it ensures no effect will be declared when no effect exists. More formally, underIn statistical terms, the intention-
to-treat analysis provides a valid—
though perhaps underpowered—α-
level test of the null hypothe-
sis of no average treatment effect
in double-blind placebo-controlled
randomized experiments.
the sharp causal null hypothesis and the exclusion restriction, it can be shown
that Pr[Y = 1|Z = 1]/ Pr[Y = 1|Z = 0] = Pr[Y
a=1
= 1]/ Pr[Y
a=0
= 1] = 1.
However, this equality is not true when the exclusion restriction does not hold,
as represented in Figure 22.1. In those cases—experiments that are not double-
blind placebo-controlled—the effect of A may be null while the effect of Z is
non-null. To see that, mentally erase the arrow A −→ Y in Figure 22.1: there
is still an arrow from Z to Y .
A related justification for the intention-to-treat effect is that its value is
“closer to the null than the value of the per-protocol effect”. The intuition is
that, if imperfect adherence results in an attenuation—not an exaggeration—of
the effect, the intention-to-treat risk ratio Pr[Y = 1|Z = 1]/ Pr[Y = 1|Z = 0]
will have a value between 1 and that of the per-protocol risk ratio Pr[Y
a=1
=
1]/ Pr[Y
a=0
= 1]. The intention-to-treat effect could thus be interpreted as a
lower bound for the per-protocol effect, i.e., the intention-to-treat effect is a
conservative estimate of the per-protocol effect. Unfortunately, the intention-
302 Target trial emulation
Fine Point 22.3
Na¨ıve per-protocol analyses. In randomized trials, two common approaches to attempt to estimate the per-protocol
effect of treatment A are “as treated” and so-called “per protocol” analyses.
A conventional as-treated analysis compares the distribution of the outcome Y in those who received treatment
(A = 1) versus those who did not receive treatment (A = 0), regardless of their treatment assignment Z. Clearly, a
conventional as-treated comparison will be confounded if the reasons that moved participants to take treatment were
associated with prognostic factors U that were not measured, as in Figures 22.1 and 22.2. On the other hand, consider
a setting in which all backdoor paths between A and Y can be blocked by conditioning on measured factors L, as in
Figure 22.3. Then an as-treated analysis needs to adjust for the factors L.
A conventional per-protocol analysis—sometimes referred to as an on-treatment analysis—only includes individuals
who adhered to the study protocol: the so-called per-protocol population of participants with A = Z. The analysis
then compares, in the per-protocol population only, the distribution of the outcome Y in those who were assigned to
treatment (Z = 1) versus those who were not assigned to treatment (Z = 0). That is, a conventional per-protocol
analysis is just an intention-to-treat analysis restricted to the per-protocol population. This restriction will generally
result in a biased estimate of the per-protocol effect. To see why, consider the causal diagram in Figure 22.4, which
includes an indicator of selection S into the per-protocol population: S = 1 if A = Z and S = 0 otherwise. Unless the
per-protocol analysis appropriately measures and adjusts for the factors L, selection bias will arise because conditioning
on S = 1 opens the noncausal path Z → A ← L ← U → Y .
That is, as-treated and per-protocol analyses are observational analyses of a randomized experiment and, like any
observational analysis, require appropriate adjustment for confounding and selection bias to obtain valid estimates of
the per-protocol effect. For examples and additional discussion, see Hern´an and Hern´andez-D´ıaz (2012).
to-treat effect is not always conservative, because an attenuated effect is not
guaranteed. See Fine Point 22.4
Even in settings in which the intention-to-treat is conservative, that mayThe argument against conservative
intention-to-treat analyses applies
to non-inferiority trials, in which the
goal is to show that one treatment
is not inferior to the other.
not be a good thing. Suppose that the goal is evaluating a treatment’s safety:
one could na¨ıvely conclude that a treatment A is safe because the intention-
to-treat effect of Z on the adverse outcome is close to null, even if treatment A
causes the adverse outcome in a significant fraction of patients. The explana-
tion may be that many individuals assigned to Z = 1 did not take, or stopped
taking, treatment before developing the adverse outcome. Then the intention-
to-treat effect would be a dangerous way to define the effect of treatment.
In summary, exclusive reliance on intention-to-treat effect estimates is hard
to justify for randomized trials with substantial non-adherence and for those
evaluating harms rather than benefits. The per-protocol effect is often a more
natural estimand for researchers and decision makers (e.g., clinicians, patients).
Estimating the per-protocol effect requires adjustment for confounding under
Figure 22.3 the assumption of exchangeability conditional on the measured covariates, or
under alternative assumptions such as those required for instrumental variable
estimation (see Chapter 16).
Figure 22.4
The above discussion revolved largely around time-fixed treatments. When,
as often happens, the randomized trial studies sustained strategies under which
treatment can vary over time, the probability of non-adherence increases greatly.
Then the intention-to-treat becomes increasingly noninformative compared
with the per-protocol effect, defined as the effect that would have been ob-
served if everyone had adhered to their assigned treatment strategy throughout
the follow-up. Estimating the per-protocol effect for sustained strategies, both
in a true randomized trial and in an observational analysis that emulates it,
generally requires g-methods.
22.2 A target trial with sustained treatment strategies 303
Fine Point 22.4
More misunderstandings about the intention-to-treat effect. A commonly heard argument is that the intention-
to-treat effect measures treatment’s effectiveness in the real world because it incorporates the fact that people will not
perfectly adhere to the assigned treatment. In contrast, the per-protocol effect would measure treatment’s efficacy under
perfect adherence to treatment. Using this terminology, it is often argued that “efficacy” does not reflect a treatment’s
effect in real conditions, and thus one is justified to report the intention-to-treat effect as the primary finding from a
randomized experiment because “effectiveness” is the most realistic measure of a treatment’s effect.
This reasoning is problematic for several reasons. First, the intention-to-treat effect measures the effect of assigned
treatment under the adherence conditions observed in a particular experiment. The actual adherence in real life may be
different (e.g., participants in a study may adhere better if they are closely monitored), and may actually be affected
by the findings from that particular experiment (e.g., people will be more likely to adhere to a treatment after they
learn it works). Second, if effectiveness is the goal, we should refrain from conducting double-blind placebo-controlled
randomized clinical trials because, in real life, both patients and doctors are aware of the received treatment and no
placebos are used. A true effectiveness measure should incorporate the effects stemming from assignment awareness
(e.g., behavioral changes) that are eliminated in double-blind randomized experiments. Third, individuals who are
planning to adhere to the treatment prescribed by their doctors will be more interested in the per-protocol effect than
in the intention-to-treat effect.
Another common argument is that the intention-to-treat effect is guaranteed to be conservative. This is not true in
all settings. If the per-protocol effect of treatment is not monotonic (i.e, not in the same direction for all individuals; see
Technical Point 5.2) and the degree of non-adherence is high, then the per-protocol effect may be closer to the null than
the intention-to-treat effect. Even for monotonic effects, the intention-to-treat effect is not necessarily conservative in
head-to-head trials in which individuals are assigned to one of two active treatments. Suppose individuals with a painful
disease were randomly assigned to either an expensive drug (Z = 1) or ibuprofen (Z = 0). The goal was to determine
which drug results in a lower risk of severe pain Y after 1 year of follow-up. Unknown to the investigators, both drugs
are equally effective to reduce pain, i.e., the per-protocol risk ratio is 1. However, adherence to ibuprofen happened
to be lower than adherence to the expensive drug because of a mild side effect that could be easily palliated. As a
result, the intention-to-treat risk ratio was greater than 1, and the investigators wrongly concluded that ibuprofen was
less effective than the expensive drug to reduce severe pain. For more details, see the discussion by Robins (1998b) and
Hern´an and Hern´andez-D´ıaz (2012).
22.2 A target trial with sustained treatment strategies
We are now ready to discuss target trials that compare sustained treatment
strategies. Because the ultimate goal is to emulate these trials using real
world observational data, we will only consider pragmatic trials with features
that resemble the real world. In particular, participants and their treating
physicians need to be aware of the treatment they receive (i.e., the treatment
assignment is not blinded), nobody receives a placebo (i.e., both strategies g
and g
′
involve either active treatments or no treatment), and participants are
monitored as frequently and intensely as regular patients outside of the study.
A trial with pragmatic features is preferable when the goal is quantifying the
effects of treatment strategies under realistic conditions.
To fix ideas, consider a randomized trial to estimate the effect of antiretrovi-
ral therapy on the 5-year risk of death among individuals with HIV infection.
Eligible participants—18 years and older, no AIDS, no previous use of an-
tiretroviral therapy—are randomly assigned to either treatment strategy g or
treatment strategy g
′
at the start of follow-up k = 0 (baseline). Their follow-up
starts at the time of assignment and ends at death (the outcome of interest),
loss to follow-up, or 60 months after baseline, whichever occurs earlier.
304 Target trial emulation
Let A
k
take value 1 if the individual receives therapy at time k and 0
otherwise, for k = 0, 1, 2...K with K = 59. Our trial will assign eligible
individuals to either the strategy g
1
“receive treatment A
k
= 1 continuously
during the follow-up unless a contraindication or toxicity arises” or the strategy
g
0
“receive treatment A
k
= 0 continuously during the follow-up”. Let the
assignment indicator Z takes value 1 if the individual is assigned to g
1
and 0
if assigned to g
0
. Let D
k
be an indicator for death (1: yes, 0: no) and C
k
anIn previous chapters we considered
the causal effect of treatment on an
outcome Y measured at the end of
follow-up. In this trial, the outcome
is a failure time, i.e., time to death
(see Technical Point 21.10).
indicator for censoring (1: yes, 0: no) by month k = 1, 2...K + 1.
Let us now define the intention-to-treat and per-protocol effects in a ran-
domized trial with sustained treatment strategies. Additional contrasts of sus-
tained strategies—referred to as direct effects—are described in Technical Point
22.1.
The intention-to-treat effect is contrast of the static strategies
• (z = 1, ¯c
K
=
¯
0): be assigned to strategy g
1
at baseline and remain under
study until the end of follow-up
• (z = 0, ¯c
K
=
¯
0): be assigned to strategy g
0
at baseline and remain under
study until the end of follow-up
The intention-to-treat effect at time k can then be expressed as the contrast
of the counterfactual risks of death Pr
h
D
z=1,¯c
k
=
¯
0
k
= 1
i
− Pr
h
D
z=0,¯c
k
=
¯
0
k
= 1
i
under assignment to strategy g
1
versus g
0
if nobody had been lost to follow-up
through time k (¯c
k
=
¯
0).
In some randomized trials, assignment to and initiation of the treatment
strategies occur simultaneously. That is, all individuals assigned to strategy g
1
start to receive treatment at time 0, regardless of whether they continue taking
it after baseline, and no individuals assigned to strategy g
0
receive treatment
at time 0, regardless of whether they start taking it after baseline. In those
cases, the intention-to-treat effect is not only the effect of assignment but also
the effect of initiation of treatment Pr
h
D
a
0
=1,¯c
k
=
¯
0
k
= 1
i
−Pr
h
D
a
0
=0,¯c
k
=
¯
0
k
= 1
i
.
Like in any randomized trial, some participants will deviate from the proto-
col by not adhering to their assigned strategy. During the follow-up, some indi-
viduals assigned to g
1
will stop treatment for no clinical reason, some individu-
als assigned to g
0
will start treatment, some individuals will use non-approved
concomitant treatments, etc. The intention-to-treat effect is agnostic about
these protocol deviations, which are the result of decisions made after base-
line. This agnosticism implies that the magnitude of the intention-to-treat
effect may heavily depend on the particular patterns of protocol deviations
that occur during the conduct of each trial. Two studies with the same pro-
tocol but conducted in different settings may have different intention-to-treat
effect estimates and neither of them is biased. Due to the limitations of the
intention-to-treat effect, we want to complement it with the per-protocol effect.
The per-protocol effect is defined by a contrast of the outcome distribution
under the interventions:
• receive treatment strategy g
1
continuously between baseline k = 0 and
end of follow-up
• receive treatment strategy g
0
continuously between baseline k = 0 and
end of follow-up
The per-protocol effect at time k can then be expressed as the contrast of the
counterfactual risks of death Pr
h
D
g
1
,¯c
k
=
¯
0
k
= 1
i
−Pr
h
D
g
0
,¯c
k
=
¯
0
k
= 1
i
under full
22.2 A target trial with sustained treatment strategies 305
Technical Point 22.1
Controlled direct effects. Consider the average causal effect of a treatment A on an outcome Y when a mediator M
is set to a particular value. We refer to this quantity as the direct effect of A on Y not through M. If the mediator
M could take two values (0 or 1), then we can define the direct effect of A on Y when M is set to 1 and the direct
effect of A on Y when M is set to 0. On the additive scale, these two direct effects are defined by the counterfactual
differences E
Y
a=1,m=1
−E
Y
a=0,m=1
and E
Y
a=1,m=0
−E
Y
a=0,m=0
, respectively. These direct effects, which
are often referred to as average controlled direct effects, could, in principle, be identified by conducting an experiment
with sequential randomization for both treatment A and mediator M, or by emulating such target experiment using
observational data. Technical Point 22.2 describes other types of direct effects for which no target experiment exists.
Suppose we conduct a randomized experiment in which participants are randomly assigned at baseline to either
treatment A = 1 or A = 0 and one month after baseline to either treatment M = 1 or M = 0. Thus all individuals will
be placed in one of four groups: (A = 1, M = 1), (A = 1, M = 0), (A = 0, M = 1), or (A = 0, M = 0). The outcome
of interest Y is measured at 3 months in all individuals (for simplicity, suppose no individuals were lost to follow-up or
died). This study design allows us to consistently estimate the controlled direct effects because the randomization of
both A and M ensures that the counterfactual quantities E [Y
a,m
] = Pr [Y
a,m
= 1] are consistently estimated by the
observed risks Pr [Y = 1|A = a, M = m].
The controlled direct effects can also be validly estimated in observational studies as long as the identifiability
conditions of consistency, positivity, and exchangeability hold for both A and M. A precise characterization of these
identifiability conditions was actually provided in Chapter 19 because a controlled direct effect is just a particular case
of a contrast of treatment strategies sustained over time. To see so, simply replace A and M by A
0
and A
1
in the
above expressions. More generally, both the treatment A and the mediator M can be time-varying themselves.
adherence to strategy g
1
versus g
0
if nobody had been lost to follow-up through
time k (¯c
k
=
¯
0).
Sensible trial protocols will not mandate that treatment be continued no
matter what happens to the individual. For example, our strategy g
1
of contin-
uous treatment mandates treatment discontinuation when a contraindication
or toxicity arises. That is, the per-protocol effect generally involves the com-
parison of dynamic strategies (“do this, if X happens then do this other thing”)
rather than static strategies (“do this, no matter what happens”).
Sometimes the study protocol is not explicit about the dynamic nature of
the treatment strategies. For example, the protocol may simplify the descrip-
tion of strategy g
1
as “receive treatment A
k
= 1 continuously during the follow-
up” without explicitly stating that the therapy must be discontinued “whenIdeally, to avoid confusions about
what should or should not be
deemed as nonadherence through-
out the follow-up, the protocol
would fully specify the treatment
strategies of interest. Then the
per-protocol effect would be well-
defined (Hern´an and Robins, 2017).
a contraindication or toxicity arises”. This simplified description of strategy
g
1
may lead to misunderstandings. Specifically, an individual assigned to g
1
who discontinues therapy because of toxicity should not be labeled as someone
who is not adhering to strategy g
1
. In fact, that person is perfectly adhering
to strategy g
1
as (it should have been) stated in the protocol. When doing
otherwise is not an option in the real world, discontinuation of the originally
assigned treatment or initiation of other medically indicated treatments can-
not possibly be considered a deviation from protocol. Because the per-protocol
effect is defined by a contrast of realistic strategies, it is particularly relevant
for causal inference research which seeks to provide evidence for decisions in
the real world.
In fact, the per-protocol effect is often the implicit target of inference. For
example, often investigators question the fidelity of the interventions imple-
mented in the study to the interventions described in the protocol, and say
that there is “bias”. This language indicates that the investigators are really
306 Target trial emulation
Technical Point 22.2
Pure direct effects and principal stratum direct effects. Besides the controlled direct effects described in Technical
Point 22.1, there exist other definitions of the average direct effect of a treatment A on an outcome Y when a potential
mediator M is set to a particular value.
The pure direct effect (also known as natural direct effect) of A on Y not through M is the average causal effect of
A on Y if the value of M had been set to the value that M would have taken if A had been set to 0, i.e., if M had
been set to the value M
a=0
(which is 1 for some individuals and 0 for others). The pure direct effect, defined by the
contrast E
h
Y
a=1,M
a=0
i
−E
h
Y
a=0,M
a=0
i
, is a cross-world quantity because E
h
Y
a=1,M
a=0
i
includes a counterfactual
outcome simultaneously indexed by both a = 1 and a = 0. Therefore, the pure direct effect cannot be identified from a
randomized experiment on A, M , or both, and cannot be identified from observational data under an FFRCISTG model
(see Technical Point 6.2). Nonetheless, estimation of pure direct effects is often the goal of causal mediation analyses
because total treatment effects can be decomposed into pure direct and total indirect effects. Pure direct effects were
introduced by Robins and Greenland (1992); Pearl (2001) renamed them as natural direct effects and showed that,
for certain causal graphs, the pure direct effect can be identified from the observed data under his NPSEM-IE model
because, unlike the FFRCISTG model, the NPSEM-IE model assumes untestable cross-world independencies that cannot
be refuted from randomized experiments on A, M, or both. For a review, see the book by VanderWeele (2015).
The principal stratum direct effect of A on Y if the value of M had been set to m is the average causal effect of
A on Y in the subset of the population whose value of M would have been equal to m regardless of the value of A,
i.e., in the subset of the population with M
a=0
= M
a=1
= m. Then the principal stratum direct effect is defined
by the contrast E
Y
a=1,m
|M
a=0
= M
a=1
= m
− E
Y
a=0,m
|M
a=0
= M
a=1
= m
. Interestingly, this is equal to
E
Y
a=1
|M
a=0
= M
a=1
= m
−E
Y
a=0
= 1|M
a=0
= M
a=1
= m
. Therefore, principal stratum direct effects do not
involve joint counterfactuals Y
a,m
, just the counterfactuals Y
a
in a subset of the population so, in that sense, they are
the total (rather than direct) effect of treatment in that subset of the population. It follows that, unlike controlled or
pure direct effects, principal stratum direct effects do not require that interventions on M are well-defined. Principal
stratum direct effects have little policy relevance when A affects M in almost all individuals, because then they apply
to the very small subset of the population with M
a=0
= M
a=1
. In practice, M is often coarsened (typically into a
binary indicator) to increase the size of the principal stratum, but coarsening itself may make the principal stratum direct
effect less scientifically relevant (Robins et al. 2007). Principal stratum direct effects were introduced by Robins (1986)
and popularized by Rubin (2004). Frangakis and Rubin (2002) following Robins (1986), used the concept of principal
stratum as a tool to handle competing events. In Chapter 23, we consider an interventionist theory of mediation (Robins
and Richardson 2010) which offers yet another type of direct effect.
interested in comparing the interventions implemented during the follow-up
as specified in the protocol (i.e., the per-protocol effect) and not in the ef-
fect of assignment to the interventions at baseline (i.e., the intention-to-treat
effect) because nonadherence after baseline cannot possibly bias the effect of
assignment at baseline.
Finally, let us consider the effect of receiving interventions other than the
ones specified in the study protocol. Suppose that, while our trial is being
conducted, a consensus started to emerge that strategy g
0
“receive treatment
A
k
= 0 continuously during the follow-up” is inferior to strategy g
1
. Therefore
some physicians began to recommend initiation of therapy when the clini-
cal course worsened when the CD4 cell count (L
k
) first dropped below 200
cells/µL. As a result, many individuals in the trial who were assigned to strat-
egy g
0
actually followed the modified strategy g
′
0
“receive treatment A
k
= 0
continuously during the follow-up but, after L
k
< 200, switch to treatment
A
k
= 1”. The contrast of outcome distributions under the interventions
• receive treatment strategy g
1
continuously between baseline k = 0 and
end of follow-up
22.3 Emulating a target trial with sustained strategies 307
• receive treatment strategy g
′
0
continuously between baseline k = 0 and
end of follow-up
corresponds to neither the intention-to-treat effect nor the original per-protocol
effect. Rather, it is a question about the per-protocol effect in a hypothetical
target trial in which individuals are randomized to either strategy g
1
or g
′
0
.
This example illustrates how causal effects of interest that do not corre-
spond to the original per-protocol effect can be conceptualized as per-protocol
effects in target trials that can be emulated using the randomized trial data.
Interestingly, if the strategies of interest differ from those in the actual trial,
it is actually disadvantageous to have all participants in the actual trial ad-
here to the strategies specified in the protocol. Complete adherence implies
that the trial data cannot be used to emulate a target trial with a different
protocol (because no individuals followed the protocol of the new target trial
in the actual data). For example, a randomized trial with full adherence in
which individuals with HIV are assigned to different CD4 cell count thresholds
at which to initiate antiretroviral therapy is of little use to emulate a trial in
which individuals are assigned to either continuous treatment or no treatment,
and vice versa. It is precisely the noncompliance that allows us to use the data
from a given randomized trial to emulate other randomized trials that answer
different, perhaps more relevant, causal questions.
In randomized trials with sustained treatment strategies, estimating per-
protocol effects raises the same issues as any comparison of sustained strategies
in an observational study. As we discuss later, valid estimation of the per-See Hern´an and Robins (2017) for
more details about the estimation
of per-protocol effects in random-
ized trials.
protocol effect generally demands that trial investigators collect post-randomization
data on adherence to the strategy and on time-varying prognostic factors as-
sociated with adherence.
22.3 Emulating a target trial with sustained strategies
If conducting a pragmatic randomized trial is not possible, we may attempt to
emulate it through the analysis of existing observational data. We then refer
to the trial as the target trial for our observational analysis.
Specifying the protocol of the target trial is a useful device to clarify the
causal question of interest that we wish our observational analysis to answer.
At the very least, we need to specify the following key components of the
protocol: eligibility criteria, start and end of follow-up, treatment strategies,
outcomes of interest, causal contrast, and data analysis plan. Note that a
precise specification of the protocol of the target trial may require some explo-
ration of the available data. For example, only after having determined that
the data included information on HIV diagnosis, can we reasonably propose to
emulate a target trial of individuals with HIV.
Analogs of the causal effects described in the previous sections for random-
ized trials can be proposed for observational analyses that emulate a target
trial.
Emulating an intention-to-treat effect is rarely possible in observational
analyses of existing data because the actual assignment to a treatment strategy
is unknown. In our example, the closest observational analog of the intention-
to-treat effect is a comparison of initiation of the different treatment strategies.
A comparison of initiators parallels the intention-to-treat analysis in target tri-
als in which assignment and initiation of the treatment strategies always occur
308 Target trial emulation
together at baseline, regardless of whether individuals continue on the strate-
gies after baseline. We can define this observational analog of the intention-to-If we had data on prescription
(rather than dispensing) of an-
tiretroviral therapy, a comparison of
groups according to whether they
did or did not receive a prescrip-
tion of therapy at baseline would be
somewhat more analogous to the
intention-to-treat analysis in the
target trial.
treat effect by a contrast of the outcome distribution under the hypothetical
interventions
• initiate treatment A
0
= 1 at baseline and remain under study until the
end of follow-up
• initiate treatment A
0
= 0 at baseline and remain under study until the
end of follow-up
This observational analog of the intention-to-treat effect at time k can then
be expressed as the contrast of the counterfactual risks Pr
h
D
a
0
=1,¯c
k
=
¯
0
k
= 1
i
−
Pr
h
D
a
0
=0,¯c
k
=
¯
0
k
= 1
i
. Unlike a true intention-to-treat effect that defines the
groups according to assigned strategy, this contrast defines them according
to initiation of each strategy. If we were using this contrast in a randomized
trial, we would be including in the same group all individuals who did not take
any dose of treatment at baseline, regardless of whether they were assigned
to strategy g
1
or g
0
. If initiation of treatment occurs shortly after assign-An observational analysis that com-
pares initiators is equivalent to the
modified intention-to-treat analysis
described in Fine Point 22.2
ment to treatment, our observational analog roughly preserves a key feature of
the intention-to-treat effect: the contrast is defined by interventions occurring
shortly after baseline.
An observational analog of the per-protocol effect, on the other hand, is
defined identically as that for the target trial. In randomized trials we differ-
entiated between the original per-protocol effect and the per-protocol effects in
alternative target trials. In observational studies this difference is unnecessary
because, in the absence of a pre-specified protocol, each per-protocol effect
corresponds to a particular target trial. In general, we can only use observa-
tional data to emulate target trials whose intended interventions are actually
followed by at least some individuals in the study. In some settings, however,
investigators may be willing to use modeling dose-response structural models,
to extrapolate beyond the interventions that are actually present in the data.
Defining the causal effects in observational studies in reference to those in
the target trial forces us to be explicit about the strategies that are compared.
This explicit specification of the treatment strategies prevents bias because it
makes it obvious that certain data analyses involve comparisons that cannot
be translated into a contrast between hypothetical interventions. These data
analyses should therefore be avoided when the goal of the analysis is to help
decision makers choose one of several courses of action, as we discussed in
Sections 3.5 and 3.6.
Another advantage of an explicit definition of the treatment strategies in
observational analyses is clarity. As discussed in Fine Point 22.4, some in-
vestigators insist in classifying causal effects into either “efficacy ” (loosely
defined: the effect of treatment that would be observed under perfect condi-
tions) or “effectiveness” (loosely defined: the effect of treatment that would be
observed under realistic conditions). Sometimes the intention-to-treat effect in
a randomized trial is interpreted as the effectiveness of treatment and the per-
protocol effect in the same trial as the efficacy of treatment. Other times the
intention-to-treat effect in a randomized trial is interpreted as efficacy (even
under imperfect conditions such as non-adherence) whereas the per-protocol
effect in the observational study that emulates it is interpreted as effectiveness
(even under perfect adherence). That is, especially in settings with sustained
22.4 Time zero 309
strategies over long periods, the labels “effectiveness” and “efficacy” are am-
biguous: it is often difficult to argue that either an intention-to-treat effect
in a setting with nonadherence or a per-protocol effect in a real world setting
measures the causal effect of treatment under perfect conditions.
Rather than insisting on an artificial efficacy-effectiveness dichotomy, it may
be more helpful to accept that all causal effects are placed somewhere along the
effectiveness continuum. An explicit definition of the treatment strategies that
define the causal effect of interest is then more informative because decision
makers need information about the effect of well-defined interventions.
22.4 Time zero
A crucial component of target trial emulation is the determination of the start
of follow-up, also referred to as baseline or time zero, in the observational
analysis. Eligibility criteria need to be met at that point but not later; study
outcomes begin to be counted after that point but not earlier.
In randomized experiments, the time zero for each individual is the time
when they are assigned to a treatment strategy while meeting the eligibil-
ity criteria. For example, in our randomized trial of antiretroviral therapy,
time zero is the time when the treatment strategies are assigned (the time
of randomization), which usually occurs shortly before, or at the same time
as, treatment is initiated. We do not start the follow-up, say, 2 years before
or after treatment assignment. Starting before randomization would not be
reasonable because the treatment strategies had yet to be assigned and the
eligibility criteria have not yet been defined, much less met; starting follow-up
after randomization is potentially biased as deaths during the first two years
of the trial would be excluded from the analysis and any short-term effects of
treatment would be missed. Even more problematic, if treatment does indeed
have a short-term effect, then more susceptible individuals would have died by
year 2 in the group assigned to active treatment but not in the other group.
This differential proportion of susceptible individuals after two years destroys
the baseline comparability achieved by randomization and opens the door to
selection bias.
The same rules regarding time zero apply to observational analyses and
randomized trials, and for the same reasons. Generally, the follow-up in the
observational analysis should start at the time the follow-up would have started
in the target trial. Otherwise the effect estimates may be hard to interpret and
biased because of selection affected by treatment. Nonetheless, in observational
studies for causal inference, errors in the emulation of time zero of the targetExample: The highly publicized dis-
crepancy between the estimates of
the effect of postmenopausal hor-
mone therapy on heart disease in
observational studies and a ran-
domized trial was partly due to mis-
handling of time zero in the former
(Hern´an et al. 2008).
trial are very frequent. These errors occur because of two common problems:
1) sometimes there is not a unique choice of time zero, and 2) sometimes
the treatment strategies cannot be uniquely assigned at time zero. We now
describe solutions for each of these two problems.
First, the problem of non-unique time zero. Consider two scenarios, ac-
cording to how many times the eligibility criteria can be met throughout an
individual’s lifetime:
1. Eligibility criteria can be met at a single time. This is the simplest
setting. Follow-up starts at the only time the eligibility criteria are met.
For example, consider a study in persons with HIV to compare immediate
initiation of antiretroviral therapy when the CD4 cell count first drops
310 Target trial emulation
below 500 cells/µL versus delayed initiation when the CD4 cell count first
drops below 350 cells/µL. The follow-up of eligible individuals starts the
first time their CD4 cell count drops below 500.
2. Eligibility criteria can be met at multiple times. This is the situation
that often leads to confusion. For example, consider a study to compare
initiation versus no initiation of hormone therapy among postmenopausal
women with no history of chronic disease and no use of hormone therapy
during the previous two years. If a woman meets these eligibility criteria
continuously between age 51 and 65, when should her follow-up start?
At age 51, 52, 53. . . ? In the target trial a woman would be eligible to
be recruited at multiple times during her lifetime, i.e., she has multiple
eligible times.
In settings with multiple eligibility times, there are several alternatives to
choose the time zero of each individual among her eligible times. One could
choose as time zero: a) the first eligible time, b) a randomly chosen eligible
time, c) every eligible time, etc. Strategy c) requires emulating multiple sequen-
tial target trials, each of them with a different start of follow-up. The number
of sequential trials depends on the frequency with which data on treatment
and covariates are collected:
• If fixed schedule for data collection at pre-specified times (e.g., every
two years, like in many epidemiologic cohorts), then emulate a new trial
starting at each pre-specified time.
• If subject-specific schedule for data collection (e.g., electronic medical
records), then choose a fixed time unit (e.g., a day, week or month), andAn unbiased choice of time unit can
vary from study to study. For ex-
ample, consider a study in which
both the time-varying treatment
and confounders change more then
once a week for many individuals.
Then choosing a week or a month
as the time unit will introduce bias.
This bias could be eliminated by us-
ing by the choice of a day as the
unit of time. If daily data on treat-
ment and confounders are not avail-
able, the bias could not be fully cor-
rected.
emulate a new trial starting at each time unit.
From a statistical standpoint, the sequential emulation strategy c) can be
more efficient than the previous ones because it uses more of the available
data. However, because individuals may be included in multiple target trials,
appropriate adjustment of the variance of the effect estimate is required. This
can be achieved by bootstrapping the entire analysis.
Second, let us talk about how to tackle the impossibility of assigning a
unique treatment strategy to each individual. Consider a target trial in which
individuals whose CD4 cell count just dropped below 500 cells/µL are assigned
to one of the following strategies: (1) start therapy immediately, (2) start
therapy when CD4 cell count drops below 350 cells/µL, (3) start therapy when
CD4 cell drops below 200 cells/µL. When emulating this target trial using
observational data, we will find individuals who started therapy at time zero
(i.e, when their CD4 cell count first dropped below 500 cells/µL) and therefore
we will assign them to strategy (1). Other individuals, however, did not start
therapy at time zero, which means that their data are compatible with following
both strategy (2) and strategy (3) at baseline. Which strategy should we assign
them to?
One possibility is to choose a single strategy at random and assign them to
that strategy, but that would be statistically inefficient. Another possibility is
to create two exact copies—clones—of each of these individuals in the data and
assign each of the two clones to a different strategy. Clones are then censored
at the time their data stop being consistent with the arm they were assigned
to. For example, if the individual does not start therapy when CD4 drops to
350, then the clone assigned to “start therapy when CD4 cell count drops to
22.5 A unified approach to answer What If questions with data 311
Fine Point 22.5
Grace periods. Consider a trial to compare immediate initiation of antiretroviral therapy at time zero versus delayed
initiation. In the real world, antiretroviral therapy cannot be started exactly on the same day that it is assigned.
Depending on the health care system, it may take weeks or months until the requisite clinical and administrative
procedures are completed and patients are adequately informed. Therefore, investigators need to define a grace period
(say, 3 months) after time zero during which initiation is still considered to be immediate. Otherwise the study would be
estimating the effect of strategies that do not occur frequently in reality or that could not be successfully implemented
in practice.
A consequence of using a grace period is that an individual’s observed data is consistent with more than one strategy
for the duration of the grace period. For example, in the above study, the introduction of a 3-month grace period implies
that the interventions are redefined as “initiate therapy within 3 months of time zero cells/µL” versus “never initiate
therapy”. Therefore individuals who start therapy in month 3 after baseline have data consistent with both strategies
during months 1 and 2. Had some of them died during those 2 months, to which strategy should we have assigned
those deaths? As described in the text, we could randomly assign these individuals to one of the two strategies or,
better, we could create two clones of each individual and assign each of the two clones to a different strategy. Clones
are censored when their data are no longer compatible with their assigned strategy. For example, if the individual starts
therapy in month 3, then the clone assigned to “start after 3 months” would be censored at that time. The potential
bias introduced by censoring can be handled via IP weighting.
When using grace periods with cloning and censoring, the intention-to-treat effect cannot be estimated because almost
everyone will contribute a clone to each of the treatment strategies. Because each individual is assigned to all strategies
at baseline, a contrast based on baseline assignment (i.e., an “intention-to-treat analysis”) will compare groups with
essentially identical outcomes. Therefore, analyses with grace period at baseline are geared towards estimating some
form of per-protocol effect and thus will generally need to incorporate adequate adjustment.
Finally, note that a well-defined initiation strategy with a grace period should specify the timing of initiation during
the grace period. For details, see the Appendix in Cain et al. (2010).
350” would be censored at that time. The potential bias introduced by this
likely informative censoring would need to be corrected by adjusting for time-
varying factors via IP weighting. Importantly, if the individual had died beforeFor a description of the cloning +
censoring + weighting procedure,
see Robins et al. (2008) and Cain
et al. (2010). For related work, see
van der Laan and Petersen (2007).
either clone was censored, then both clones would have died and therefore the
death would have been assigned to both strategies. This double allocation of
events prevents the bias that could arise if events occurring during the waiting
period were systematically assigned to one of the two strategies only.
Again, because individuals may be included multiple times in the analysis
via their clones, appropriate adjustment of the variance of the effect estimate
is required via bootstrapping. The cloning + censoring + weighting procedure
can be combined with sequential target trial emulation when the eligibility
criteria can be met at multiple times. Fine Point 22.5 describes the handling
of strategies that can be initiated during a grace period after time zero rather
than exactly at time zero.
22.5 A unified approach to answer What If questions with data
This book describes and integrates two causal inference frameworks: counter-
factuals and causal diagrams. Explicit target trial emulation recapitulates both
frameworks and grounds them to actionable causal inference. By organizing
causal inference around a deeply familiar scientific concept—the experiment—
312 Target trial emulation
the target trial framework helps investigators use their subject-matter knowl-
edge to articulate well-defined causal inference questions. Once the causal
question is stated with little ambiguity, study design and data analysis flow
naturally.
The target trial framework is applicable to a wide range of causal ques-
tions across many disciplines, regardless of the terminology and methodology
privileged in each field. For example, economists often refer to confound-
ing and conditional exchangeability as omitted variable bias and selection on
observables, respectively, and traditional social scientists are unlikely to use
g-methods because their causal questions are not typically organized around
time-varying treatments. But these disciplinary differences are superficial com-
pared with the fundamental task that all health and social scientists interested
in causal inference face: they all need to articulate their causal questions as
a contrast of well-defined counterfactuals. The target trial framework facil-
itates that task by helping define the well-defined interventions that lead to
well-defined counterfactuals.
The target trial framework also provides a common language to unify the
causal analysis of randomized and observational studies. Aside from baseline
randomization, there are no other necessary differences between analyses of
observational data that emulate a target trial and of true randomized trials
(see Fine Point 22.6). That is, a randomized trial can be viewed as a follow-up
study with baseline randomization and observational longitudinal data as a
follow-up study without baseline randomization.
The similarities between follow-up studies with and without baseline ran-
domization are increasingly apparent in the health and social sciences as a
growing number of randomized experiments attempt to estimate the effects of
sustained treatment strategies over long periods in real world settings. These
studies are a far cry from the short experiments in tightly controlled settings
that put randomized trials at the top of the hierarchy of study designs in the
mid-20th century. For causal questions involving treatment strategies sustained
over long periods, randomized experiments with the potential for substantial
deviations from protocol (e.g., imperfect adherence to the assigned strategy,
loss to follow-up) are subject to confounding and selection biases that we have
learned to associate exclusively with observational studies.
In particular, when estimating a per-protocol effect, both randomized trials
and observational studies may need adjustment for time-varying prognostic fac-
tors that predict drop-out (selection bias) and treatment (confounding). ThatTime-varying confounding in obser-
vational studies is a bias with the
same structure as nonrandom non-
compliance in randomized trials.
is, the methodology for causal inference described in this book applies equally
to the per-protocol analyses of randomized trials and observational studies.
And, for the same reasons that success is not guaranteed when estimating
causal effects from observational data, the per-protocol effect estimates from
randomized trials may be biased too.
In view of these similarities, one might expect that randomized experiments
and observational studies would be analyzed similarly, except adjustment for
baseline confounders in observational analyses to estimate the analog of the
intention-to-treat effect. In practice, however, the typical analyses of ran-
domized experiments and observational studies differ radically, which is both
perplexing and, as we argue below, problematic.
A natural question is whether the “intention-to-treat analysis” and the
so-called “per-protocol analysis” commonly used in randomized trials validly
estimate the intention-to-treat effect and per-protocol effect, respectively.
A typical intention-to-treat analysis compares the distribution of outcomes
between randomized groups without any form of adjustment for confounding
22.5 A unified approach to answer What If questions with data 313
Fine Point 22.6
How do the data of randomized experiments and observational studies differ? Only three things distinguish the
data from randomized experiments and observational studies. In randomized experiments, (i) no baseline confounding
is expected because of randomization, (ii) the randomization probabilities are known, and (iii) the assignment to a
treatment strategy is known for each individual at baseline.
An observational analysis can emulate (i) if one measures and appropriately adjusts for a sufficient set of covariates,
and (ii) if the model for treatment assignment given the past is correctly specified. Interestingly, (iii) is not necessary for
estimating the per-protocol effect in either randomized experiments or observational studies because efficient estimators
(that are functions of the sufficient statistic) do not use this information. That is, the analyst does not need to know
the strategies being compared, much less who was assigned to which strategy: in a randomized trial, you can delete
the randomization assignment from the dataset and still estimate a per-protocol effect if a sufficient set of confounders
was measured. In a trial of dynamic strategies with perfect adherence, a sufficient set is all time-fixed and time-varying
covariates used by the strategies in assigning treatment (Robins 1986).
or selection bias. Lack of adjustment for baseline confounding is justified by
randomization: the randomized groups are exchangeable because they are ex-
pected to have the same risk of the outcome if both groups had been assigned
to the same treatment strategy. No adjustment for post-randomization con-
founding (e.g., due to nonadherence) is required because, again, there cannot
be post-randomization confounding for the effect of baseline assignment.
However, baseline randomization cannot ensure exchangeability between
those who are and are not lost to follow-up after randomization. Because the
strategies that define the intention-to-treat effect require that the individu-
als remain in the study until their outcome variable can be ascertained, an
intention-to-treat effect estimate calculated among those who are not lost to
follow-up may be affected by post-randomization selection bias if prognostic
factors influence, or are associated with, differential loss to follow-up. There-
fore, valid estimation of the intention-to-treat effect may require an “intention-
to-treat analysis” adjusted for post-randomization (time-varying) prognostic
factors to eliminate selection bias from loss to follow-up. For example, in aFine Point 22.2 refers to an
intention-to-treat analysis that
does not even attempt to adjust
for selection bias as a pseudo-
intention-to-treat analysis.
randomized trial of antiretroviral therapy among HIV patients, g-methods will
be needed if the probability of dropping out of the study is influenced by the
onset of symptoms or other risk factors for the outcome.
In addition to the primary intention-to-treat analysis, many randomized
trials also report the results from a so-called per-protocol analysis restricted to
individuals who adhered to the instructions specified in the study protocol, as
described in Fine Point 22.3 for point interventions. For sustained treatment
strategies, individuals are censored at the first time they deviate from the
protocol. That is, the remaining per-protocol population at each time is the
set of individuals that are still adhering to the protocol. No adjustment of any
kind is performed. This unadjusted analysis is questionable for three reasons.Fine Point 22.3 refers to a per-
protocol analysis that does not even
attempt to adjust for confounding
as a na¨ıve per-protocol analysis.
First, like in an intention-to-treat analysis, there may be selection bias
due to differential loss to follow-up. If so, adjustment for post-baseline (time-
varying) risk factors via g-methods will be needed.
Second, the analysis partly disregards the randomized groups and therefore
the subset of individuals who remain on protocol under one strategy may not be
exchangeable with the subset on protocol under another strategy. That is, this
“per-protocol analysis” is akin to an observational analysis and thus requires
g-methods to adjust for bias due to time-varying risk factors that affect the
314 Target trial emulation
decision to stay on protocol. Instrumental variable estimation (Chapter 16)
can sometimes be used to validly estimate per-protocol effects without explicit
adjustment for any variables, but the validity of these methods depends onFor failure time outcomes, g-
methods are always needed when
the treatment has a causal effect on
the outcome. The reason is that
treatment A
k
affects all variables
after time k through its effect on
the time-varying indicator D
k+1
, as
discussed in Technical Point 21.10.
having a valid instrument and on strong modeling assumptions. Some forms
of instrumental variable estimation are a particular case of g-estimation (see
Technical Point 16.6).
Third, this conventional per-protocol analysis ignores that the sustained
treatment strategies under comparison are dynamic strategies. A common
mistake is censoring individuals who discontinue treatment as if treatment
discontinuation were, by definition, a deviation from protocol—which is why
this analysis is also known as on-treatment analysis. We have discussed above
that individuals who stop treatment because of toxicity or a contraindication
are not deviating from protocol and therefore should not be censored.
All the above considerations apply to the analysis of both randomized trials
and observational data to emulate a target trial. When the goal is estimating a
per-protocol effect or its observational analog, the analysis of randomized trials
and observational studies should be identical. If we feel compelled to adjust
for time-varying confounding and selection bias in the analysis of observational
studies, we should feel equally compelled to adjust for post-randomization
confounding and selection bias in the analysis of randomized trials. Adjustment
for time-varying factors using g-methods will generally be necessary for per-
protocol analyses of both randomized trials and observational studies. The
target trial framework and g-methods make it possible to implement a unified
approach to causal inference for sustained treatment strategies. Historically,
randomized experiments have been considered far superior to observational
studies for the purpose of making causal inferences and aiding decision-making.
Unfortunately, randomized experiments are not always available because theyUnder some extremely rare circum-
stances, decisions based on qual-
ity randomized trials may be infe-
rior to decisions based on severely
confounded observational data, as
described in Fine Points 22.7 and
22.8.
may be expensive, infeasible, unethical, or just untimely to support an urgent
decision. Therefore, as much as we value the benefits of randomization, it is a
fact that many decisions will need to be made in the absence of evidence from
randomized trials. When we cannot conduct the randomized experiment that
would answer our causal question, we resort to attempting to emulate it using
observational data. It is therefore important to use a sound approach to design
and analyze observational studies. Making the target trial explicit is one step
in that direction. When the goal is to assist decision making, the analysis of
existing observational data need to explicitly emulate a trial and be evaluated
with respect to how well they emulate their target trial.
22.5 A unified approach to answer What If questions with data 315
Fine Point 22.7
A counterintuitive comparison of a randomized trial and an observational study. An untested over-the-counter
treatment A was used by many individuals with lung cancer in a country. This worried the country’s drug regulator who,
in response, funded a double-blind placebo-controlled randomized trial of A in a random sample of 20% of individuals
diagnosed with lung cancer over the next year. All trial participants adhered to their assigned treatment. The 60-month
mortality risk was 55% in the treatment arm and 45% in the placebo arm as shown in the table below:
A = 0 A = 1
Y = 1 450 550
Y = 0 550 450
1000 1000
As a result, the regulator banned the treatment. Later, an observational study was conducted on the 80% of lung cancer
patients not selected into the trial. This study found a mortality risk of 0% in both the treated and the untreated over
the same period as the trial. How can the observational and the randomized trial data be reconciled?
Let us first remember that individuals can be classified into counterfactual types: 1) “doomed”(Y
a=0
= Y
a=1
= 1),
2) “hurt”(Y
a=0
= 0, Y
a=1
= 1), 3) “helped”(Y
a=0
= 1, Y
a=1
= 0), and 4) “immune”(Y
a=0
= Y
a=1
= 0). By
random sampling and randomization, the following three groups have the same distribution of counterfactual types:
the 1000 individuals treated in the trial, the 1000 individuals untreated in the trial, and the 8000 individuals in the
observational study. The key observayion is that the 0% mortality in the observational study implies (i) there are no
“doomed”individuals, (ii) all individuals with Y
a=1
= 1 must have been of type ”hurt” and received A = 0, and (iii) all
individuals with Y
a=0
= 1 must have been of type ”helped” and received A = 1.
We next use these observations to reconstruct the trial data by counterfactual type. As argued above, the 550 individ-
uals with A = 1 who died (Y
a=1
= 1) were of type “hurt”. By randomization there must also be 550 “hurt”individuals
with A = 0 who, of course, survived. Arguing similarly, we can fill in the table for type “helped”.
”Hurt” A = 0 A = 1
Y = 1 0 550
Y = 0 550 0
550 550
”Helped” A = 0 A = 1
Y = 1 450 0
Y = 0 0 450
450 450
Combining the two tables, we recover the overall trial data, which implies that there are no “immune”individuals.
We conclude that the regulator should relicense treatment A and recommend that the current practice be continued, as
the observational study demonstrated that somehow every individual with lung cancer had private knowledge, unavailable
to the trialists, as to whether treatment was personally harmful or beneficial. We next describe an extreme scenario
that could explain the source of this private knowledge.
Suppose that there was a 55/45 ethnic split in the population and that, for genetic reasons, the treatment was
uniformly harmful to individuals with lung cancer in the first group (i.e., all are of type ”hurt”), but was uniformly
beneficial to all individuals with cancer in the second group (i.e., all are of type ”helped”). Also suppose that, at some
time before the trial, individuals with cancer in the first ethnic group refrained from taking the treatment after having
seen several of the group’s members quickly die after taking it. Conversely, suppose all individuals with cancer in the
second ethnic group chose to take the treatment after having seen several of the group’s members survive after taking it.
In other words, suppose that there is both (i) maximal qualitative effect modification by ethnic group and (ii) maximal
confounding by ethnic group in the observational data.
The extreme setting described above is of course unrealistic, but it is useful to explain an important point: The
randomized trial compared the strategies “treat everybody”and “treat nobody”, but the optimal strategy is “treat only
individuals in ethnic group 2”. When data on the effect modifier (i.e., ethnic group) are not obtained, it is not possible
to assign individuals to the optimal strategy in a randomized trial. In contrast, in the observational study, all individuals
followed the optimal strategy and thus had the optimal outcome of no deaths. Thus, the confounded observational
study, and not the unconfounded randomized trial, revealed the correct policy.
316 Target trial emulation
Fine Point 22.8
Generalizing Fine Point 22.7 to realistic settings The above discussion can be generalized to more realistic settings
in order to show that a design in which randomized trial and observational data are combined may be more informative
than a design with randomized trial data alone, provided individuals in both the randomized and observational data are
random samples of all individuals eligible for the trial.
Suppose we conduct a randomized trial for a binary treatment A and an outcome Y in a population in which a
treatment is already in use (lower values of Y are preferable). Further suppose that, as may occasionally happen, the
mean outcome E[Y ] in the observational study is less than the mean outcome in both arms of the randomized trial,
which implies E[Y ] is less than both E[Y
a=0
] and E
Y
a=1
. Then, we might choose to leave the current community
practice with respect to the treatment unchanged.
We next demonstrate that E[Y ] = E[Y
g
] for a strategy g that differs from the strategies “treat everybody” a = 1
and “treat nobody” a = 0 compared in the trial. Specifically, let U be a sufficient set of unmeasured, possibly unknown,
pre-treatment covariates sufficient to ensure Y
a
⨿ A|U and let Pr[A = 1|U] be the associated propensity score in the
observational data. Then the above equality holds for the random strategy g in which treatment A = 1 is randomly
assigned with probability Pr[A = 1|U] , as this choice gives the random strategy g that generated the observational data
on A, Y and the unknown U . Even though the strategy g cannot be implemented because data on U is unavailable,
the above discussion could motivate the investigators to measure pre-treatment covariates V , which can be used to
analyze the randomized trial data to find and then implement a deterministic dynamic strategy g
∗
(x) such that E[Y
g
∗
],
as estimated from the unconfounded randomized trial data, is less than the observational E[Y ].
Chapter 23
CAUSAL MEDIATION
In Part III, we have presented approaches to estimate the causal effect of a time-varying treatment on an outcome.
Our goal was to quantify changes in the outcome distribution under different treatment strategies that are sustained
over time. Our goal was not to determine how treatment exerted its effect on the outcome. We now turn our
attention to causal mediation: the study of the causal pathways through which the treatment affects the outcome.
The study of causal mediation can be seen as a special case of causal inference with time-varying treatments.
Rather than having a single treatment that takes different values over time, in mediation analysis we have two
different variables—the treatment of interest and the mediator—at different times. This chapter describes a
theoretical framework for causal mediation that, like the rest of the book, is based on hypothetical interventions
that can be mapped into a target trial. Unlike other approaches to mediation that are based on pure direct effects
and total indirect effects, an interventionist framework for mediation opens the door to empirical verification of
the causal estimates, a desirable condition for any scientific endeavor.
23.1 Mediation analysis under attack
Consider a randomized trial in which a random sample of cigarette smokers
are assigned to either smoking cessation (A = 0) or to continuation of smoking
(A = 1). Suppose that there was perfect adherence: all individuals assigned
to A = 0 quit smoking and all individuals assigned to (A = 1) continued to
smoke. The investigators found a beneficial effect of smoking cessation on the
risk of myocardial infarction Y at 1 year, i.e., E [Y |A = 1] > E [Y |A = 0]
After the beneficial effect of smoking cessation A on the risk of heart dis-
ease Y has been established, the investigators wonder whether the benefit is a
consequence of the effect of A on reducing hypertension M . Besides data on
treatment A at baseline and outcome Y at one year, they also have data on the
presence of hypertension M measured at 6 months. (For simplicity, suppose
Figure 23.1
that no individual experienced the outcome Y in the first 6 months.) The
causal diagram in Figure 23.1 depicts these variables under the assumption
that interventions on M are sufficiently well defined.
Investigators are interested in decomposing the total effect of A on Y into
the indirect causal pathways mediated by M and the direct pathways not
mediated by M. We then say that investigators are interested in a causal
mediation analysis.
In the previous chapter we introduced several approaches to formalize the
concept of direct effects (Technical Points 22.1 and 22.2) but not the concept
of indirect effect. To formalize the decomposition of a total treatment intoRobins and Greenland (1992) intro-
duced the pure direct effect and the
total indirect effect.
direct and indirect effects, we can define the pure direct effect and the total
indirect effect of A on Y .
The pure direct effect of A on Y not through M is the average causal effect
of A on Y if, for each individual, the value of M had been set to the value
that M would have taken if A had been set to 0, i.e., if M had been set to the
value M
a=0
(which is 1 for some individuals and 0 for others). The pure direct
318 Causal mediation
Technical Point 23.1
Proof of the mediation formula. In the setting depicted by the causal diagram in Figure 23.1 with treatment A,
mediator M, and outcome Y , the counterfactual mean E
h
Y
a=1,M
a=0
i
is equal to
=
P
m
E
Y
a=1,m
|M
a=0
= m
Pr[M
a=0
= m] by the laws of probability
=
P
m
E
Y
a=1,m
Pr[M
a=0
= m] by the cross-world conditional independence Y
a=1,m
⊥⊥M
a=0
=
P
m
E [Y |A = 1, M = m] Pr[M = m|A = 0] by exchangeability and consistency.
The cross-world conditional independence used above is assumed when the causal diagram represents an NPSEM-IE,
but not when it represents an FFRCISTG model.
effect is then the contrast
E
h
Y
a=1,M
a=0
i
− E
h
Y
a=0,M
a=0
i
In our example, the pure direct effect is the effect of smoking cessation A if
we could assign to each person the value of hypertension M (1 or 0) that the
person would have had if she had quit smoking. This value of hypertension M
is known for individuals who actually quit smoking, but it remains unknown
for individuals who continued to smoke. We therefore say that E
h
Y
a=1,M
a=0
i
,
and therefore the pure direct effect, is a cross-world quantity because it involves
a counterfactual outcome indexed by two treatment values, a = 1 and a = 0,
that cannot occur simultaneously for the same individual in the same world.Pearl (2001) referred to the pure di-
rect effect and the total indirect ef-
fect as the natural direct effect and
the natural indirect effect, respec-
tively.
The total indirect effect, also a cross-world quantity, is defined as
E
h
Y
a=1,M
a=1
i
− E
h
Y
a=1,M
a=0
i
The sum of the pure direct effect and the total indirect effect E
h
Y
a=1,M
a=1
i
−
E
h
Y
a=0,M
a=0
i
is, by consistency, the total effect E
Y
a=1
− E
Y
a=0
.
In Figure 23.1, there do not exist unmeasured common causes of the medi-
ator M and the outcome Y . If common causes were present, no direct effects
could be identified, including controlled direct effects and the mediation effects,
i.e., the pure direct and the total indirect effects. To identify the mediation
effects, we need to identify the cross world quantity E
h
Y
a=1,M
a=0
i
under the
causal diagram in Figure 23.1. The so-called mediation formula does that:
X
m
E [Y |A = 1, M = m] Pr[M = m |A = 0]
The proof is shown in Technical Point 23.1.
The mediation formula seems surprising because it identifies a cross-world
counterfactual quantity whose value cannot be empirically confirmed by any
experimental intervention on A and M , not even in principle. To achieveIn some very unusual situations,
we could identify the value of this
cross-world counterfactual quantity
by a crossover trial (see Fine Points
2.1 and 3.2).
this, however, one needs to assume that the causal diagram in Figure 23.1
represents an NPSEM-IE rather than an FFRCISTG, the latter of which is
the counterfactual model that we have been using throughout the book (see
Technical Point 6.2).
The proof of the mediation formula requires the unverifiable assumption
that some counterfactual variables defined in separate worlds are independent.
Specifically, the proof requires that the value of the outcome Y
a=1,m
in a world
23.2 A defense of mediation analysis 319
in which we have jointly intervened by setting the value of treatment to 1 and
the value of the mediator to m is independent from the value of the mediator
M
a=0
in a world in which we have intervened to set the value of treatment
to 0. Therefore, the variables Y
a=1,m
and M
a=0
cannot be simultaneously
observed for the same individual in a single world, and thus their independence
is not empirically verifiable in any experiment in which A and M are randomly
assigned singly or jointly (see Technical Point 7.1).
These cross-world independencies are assumed under an NPSEM-IE but
not under an FFRCISTG model. This is one reason for our privileging anUnder an FFRCISTG model, the
pure direct effect and the total indi-
rect effect are not point identified,
but sharp bounds can be obtained
(Robins and Richardson 2010).
FFRCISTG model over an NPSEM-IE: because cross-world independencies
cannot be verified by any randomized experiment, we want to use causal infer-
ence methods whose results are, in principle, verifiable.
Based on this discussion, some policy makers are unimpressed that the
investigators can identify the pure direct effect. As a cross-world parameter,
they find the pure direct effect to be without policy or public health importance
because it does not correspond to any intervention. To convince these skeptics,
advocates of the NPSEM-IE will need to work harder.
23.2 A defense of mediation analysis
The investigators of the smoking cessation trial, as advocates of the NPSEM-
IE, prepare the following rationale to convince the skeptics about the practical
utility of the pure direct effect.
“Suppose that, starting a year from now, nicotine-free cigarettes
will be available and that your policy goal is learning the benefits
of nicotine-free cigarettes as soon as possible. To do so, we use
the already collected data from the above smoking cessation trial
to estimate the two-year risk of heart disease Y under an inter-
vention requiring all smokers to change to nicotine-free cigarettes
(when they become available). Suppose that strong experimentalPearl (2001) provided a similar ar-
gument to justify the use of pure
direct effects.
evidence exists that (i) the entire causal effect of nicotine on the
outcome Y (heart disease) is through its effect on the mediator
M (hypertension), and that (ii) the non-nicotine components in
cigarettes have no direct causal effect on the mediator M (hyper-
tension). Under assumptions (i) and (ii), the hypertensive status
M of a smoker of nicotine-free cigarettes will equal her hypertensive
status under non-exposure to cigarettes and hence E
h
Y
a=1,M
a=0
i
will be the risk of heart disease in smokers were all smokers to
change to nicotine-free cigarettes a year from now. That is exactly
your public health effect of interest and this is what the mediation
formula would compute when applied to the data of our study”.
This is interesting. To argue for the substantive importance of the parame-
ter E
h
Y
a=1,M
a=0
i
, the NPSEM-IE advocates tell a story about the effect of an
intervention on the nicotine content of cigarettes—an intervention that makes
no reference to the mediator M at all. Also, they make the “no direct effect”
assumptions (i) and (ii) about the absence of direct effects of variables that
were not even included on the causal diagram in Figure 23.1.
The investigators’ story states that the variable A can be decomposed into
two separable components N and O. The separable component N directly
320 Causal mediation
Technical Point 23.2
When the mediation formula is the g-formula. According to the causal diagram in Figure 23.3, exchangeability
holds for the separable components N and O and therefore the mean E
Y
n=0,o=1
may be identified by the g-formula.
However, in the smoking cessation trial described in the main text, no individual has data (N = 0, O = 1). Therefore,
positivity does not hold and it appears that the g-formula cannot identify E
Y
n=0,o=1
. But, given exchangeability and
consistency, positivity is a sufficient but not necessary condition for identification by the g-formula; identification only
requires that the g-formula is a function of the observed data distribution. We now show that the deterministic bold
arrows in Figure 23.2 and the no direct effect assumptions (i) and (ii) together imply that the g-formula is indeed a
function of the observed data distribution of (A, M, Y )—that function being the mediation formula.
Under an FFRCISTG represented by Figure 23.2, if data on N and O were available, the mean E
Y
n=0,o=1
would
be identified by the g-formula
X
m
E [Y |O = 1, M = m] Pr(M = m |N = 0)
since, in the g-formula N = 0 needs not be included in the first conditioning event and O = 1 needs not be included in
the second conditioning event because N is not a parent of Y and O is not a parent of M in Figure 23.2. Furthermore,
even though positivity does not hold, the g-formula is a function of the observed data distribution only because O = 1
if and only if A = 1 and N = 0 if and only if A = 0. Thus, we can rewrite the g-formula for E
Y
n=0,o=1
as
X
m
E [Y |A = 1, M = m] Pr(M = m |A = 0)
which is exactly the mediation formula. This derivation, based on the g-formula, is somewhat heuristic because of the
presence of null sets arising from determinism between N, O and L. Robins et al. (2022) provide an alternative, rigorous
proof using the SWIG Markov property described in Technical Point 21.12.
Not only does the g-formula equal the mediation formula under the expanded causal diagram in Figure 23.2, but the
g-formula also equals the front door formula under the expanded causal diagram in Figure 23.7, as shown in Technical
Point 23.3.
affects M but not Y . The separable component O directly affects Y but not
M. Also, according to the story, each separable component can in principle be
intervened on separately. For example, Y
n=0,o=1
represents the counterfactual
Figure 23.2
outcome under an intervention that removes (only) the nicotine component of
cigarettes.
The most direct representation of this causal story is provided by an FFR-
CISTG model represented by the causal DAG in Figure 23.2 where N is a
binary variable representing nicotine exposure, and O is a binary variable rep-
resenting exposure to the other non-nicotine components of a cigarette. The
bold arrows from A to N and O indicate deterministic relationships. This is
because, in the actual data from the trial, either one continues to smoke normal
cigarettes so A = N = O = 1, or quits smoking cigarettes so A = N = O = 0.
The absence of an arrow from N to Y encodes assumption (i) that N doesThese are “no controlled direct ef-
fect” assumptions. Assumption (i)
says that there is no direct effect of
N on Y when controlling for (set-
ting) the value of M.
not have a direct effect on Y . The absence of an arrow from O to M en-
codes assumption (ii) that O does not have an effect on M. Figure 23.3 shows
the associated SWIG. If O is not a cause of M for every individual we can
additionally write the random variable M
n,o
as M
n
.
Under this characterization of the problem, the g-formula that identifies
E
Y
n=0,o=1
is exactly the mediation formula (see proof in Technical Point
23.2). Let us review the lessons we learned.
For a researcher that initially accepted an NPSEM-IE associated with the
23.3 Empirically verifiable mediation 321
DAG in Figure 22.1, the mean E
h
Y
a=1,M
a=0
i
was already identified by the
mediation formula so the story of separable effects of N and O did not con-
tribute to identification. Rather, it served only to show that the parameter
E
h
Y
a=1,M
a=0
i
—and thus the pure direct effect and the total indirect effect—
Figure 23.3
encodes a parameter E
Y
n=0,o=1
of public health interest. For a researcher
that takes the FFRCISTG point of view, the story not only provides an inter-
ventional interpretation of the mean E
h
Y
a=1,M
a=0
i
as the mean E
Y
n=0,o=1
,
but in addition makes both means identifiable via the g-formula or, equiva-
lently, the mediation formula. In fact, when we interpret absence of an ar-
row as an absence of a direct causal effect for all individuals, Y
a=1,M
a=0
and
Y
n=0,o=1
are equal for every individual.
This characterization of the problem also allows us to define and identify the
separable direct effect of the component N on the outcome Y , E
Y
n=1,o=1
−
E
Y
n=0,o=1
, which is a controlled direct effect for the separable compo-
nent N. This effect is also equal to the total indirect effect E
Y
a=1
−
E
h
Y
a=1,M
a=0
i
. Analogously, E
Y
n=1,o=1
− E
Y
n=1,o=0
is the pure direct
effect E
h
Y
a=1,M
a=0
i
− E
Y
a=0
.
23.3 Empirically verifiable mediation
The interventional interpretation of E
h
Y
a=1,M
a=0
i
is only valid if the story
about the separable effects of N and O is correct and Figure 23.3 represents
an FFRCISTG. An advantage of the interventional interpretation is that the
validity of this story can be, in principle, empirically refuted via a randomized
trial, as we now describe.
When nicotine-free cigarettes become available in a year, we conduct a new
randomized trial in which a random sample of cigarette smokers are randomly
assigned to one of three groups: smoking cessation (A = N = O = 0), contin-
uation of smoking of standard cigarettes (A = N = O = 1), or continuation of
smoking of nicotine-free cigarettes (N = 0, O = 1). That is, the new trial has
the same two arms as the original trial plus an additional arm of nicotine-free
cigarettes. In the absence of temporal trends, the mean outcomes for the first
two arms should be the same in both trials. We assume that the sample size
of both trials is large enough to ignore sampling variability.
By randomization, the mean outcome E [Y |N = 0, O = 1] in the new trial
is expected to equal E
Y
n=0,o=1
. Therefore, if our story is correct, we expect
that E [Y |N = 0, O = 1] will equal the mediation formula from the earlier trial.
Otherwise, the N and O story has been empirically refuted, which implies that
one or more of the following assumptions is incorrect: (i) no direct effect of
nicotine on the outcome, (ii) no direct effect of other, non-nicotine components
on the mediator, (iii) no unmeasured common cause U of M and Y on the
causal diagram in Figure 23.2.
If E [Y |N = 0, O = 1] differs from the mediation formula, we can use the
data from this new trial to investigate which of the assumptions (i)-(iii) are
false. To do so, we start by checking whether O and M are associated among
those with N = 0, i.e.,
E [M|N = 0, O = 1] − E [M |N = 0, O = 0] = 0
322 Causal mediation
Fine Point 23.1
Empirical falsification of the assumptions for separable effects. Suppose we had conducted the three-arm trial
with interventions on N and O, and found that N and Y are associated within joint levels of M and O. Then, as
stated in the main text, we conclude that either assumption (i) or assumption (iii), or both, are false.
To determine which of the two assumptions are false, we would need another randomized trial with, say, 8 arms
in which we intervene on M as well as on N and O. If N has no direct effect on Y except through M, N will be
independent of Y given M and O in the eight-arm trial. If M and Y do not share an unmeasured common cause, the
conditional distribution of Y given M within levels of N and O should be the same in the three-arm trial and in the
eight-arm trial.
One might wonder how Figure 23.2 can have an unmeasured common cause of M and Y left off the graph if we
are correct in assuming that Figure 23.1 represents an FFRCISTG model with no common causes of M and Y . The
explanation is that common causes may only be present (i.e., active) under interventions that assign different values of N
and O to each person. The FFRCISTG model associated with Figure 23.1, unlike that associated with Figure 23.2, only
considers interventions A = N = O = 1 and A = N = O = 0 that assign the same value to each person. Interestingly,
if a common cause U of Y and M is the only reason E [Y |N = 0, O = 1] in the new trial differs from the mediation
formula, it is still the case that Y
n=0,o=1
= Y
a=1,M
a=0
for every individual. However, E
Y
n=0,o=1
= E
h
Y
a=1,M
a=0
i
is not identified by the mediation formula. Robins et al. (2022) describe a hypothetical but realistic study of treatment
for river blindness under which Figure 23.1 is an FFRCISTG but Figure 23.2 is not because a common cause U of Y
and M is missing from the latter graph.
If that is the case, then assumption (ii) is refuted and the arrow O → M should
be added to Figure 23.2 (and the corresponding arrow to Figure 22.3).
We next check whether N and Y are associated within joint levels of M
and O, i.e., whether
E [Y |N = 1, O = 1, M = m] − E [Y |N = 0, O = 1, M = m] = 0
for some values of m. If that is the case, then assumption (i) is refuted (which
implies that an arrow N → Y should be added to the causal diagrams) or an
unmeasured common cause U of M and Y exists (and should be added to the
causal diagrams). See Fine Point 23.1.
Now suppose that in two years, when the results of the new trial become
available, the mean outcome estimates are equal in the arms that correspond to
the same intervention in both trials, but the estimate of the mean outcome in
the third arm of the new trial, E [Y |N = 0, O = 1], differs from the mediation
formula in the first trial. How would different people react?
Both a person who had assumed that Figure 23.1 was an NPSEM-IE and
a person who only assumed that it was an FFRCISTG would agree that the
story of separable effects of O and N was incorrect, and that E
Y
n=0,o=1
is
correctly estimated by the mean outcome in the third arm of the new trial and
not by the mediation formula in the earlier trial.
Those who had assumed an NPSEM-IE can continue to believe that the
mean E
h
Y
a=1,M
a=0
i
is still equal to the mediation formula, but they cannot
justify the policy interest of the pure direct effect as the effect of taking nicotine-
free cigarettes. Those who assumed an FFRCISTG may have little interest in
the original mediation formula. Instead they will be interested in what they
have learned about the effects of nicotine-free cigarettes on the outcome from
the three-arm randomized trial. They will also be interested in learning that
one or more of the following assumptions were false: (i) no direct effect of
23.4 An interventionist theory of mediation 323
nicotine on the outcome, (ii) no direct effect of other, non-nicotine components
on the mediator, (iii) no unmeasured common cause U of M and Y .
Continue to assume that Figure 23.1 represents an FFRCISTG model and
that E
Y
n=0,o=1
in the future nicotine-free cigarette trial differs from the
mediation formula. An interesting question is whether treatment A can always
be decomposed into other (possibly unknown) intervenable components N
′
and
O
′
such that Figure 23.2 is an FFRCISTG and the no direct effect assumptionsIf E
h
Y
a=1,M
a=0
i
were always
point identified by the media-
tion formula, the sharp bounds
in Robins and Richardson (2010)
would be violated.
(i) and (ii) hold, in which case E
h
Y
n
′
=0,o
′
=1
i
would equal E
h
Y
a=1,M
a=0
i
and
both would equal the mediation formula? The answer is no, since otherwise
E
h
Y
a=1,M
a=0
i
would always be point identified by the mediation formula,
which is not the case.
23.4 An interventionist theory of mediation
In this chapter we have introduced an interventionist theory of causal medi-
ation that differs from the standard approach based on pure direct and to-This theory of interventionist medi-
ation was presented by Robins and
Richardson (2010) and extended by
Robins, Richardson, and Shpitser
(2022). The theory has been ex-
tended to survival analysis (Didelez
2019, Aalen et al. 2020), compet-
ing risks (Stensrud et al. 2020,
2021), and settings with interfer-
ence (Shpitser et al. 2021).
tal indirect effects. Because the interventionist theory was developed in re-
sponse to perceived deficiencies in the standard theory, we first described the
standard theory and its problematic aspects resting on the use of cross-world
(nested) counterfactuals. However, the interventionist theory can be viewed
as autonomous, providing a self-contained framework for discussing mediation
without reference to cross-world nested counterfactuals.
To do so, we used a (simplified) randomized trial with a time-fixed treat-
ment as an intervention. The key idea was reframing the mediation question as
a question about the effects of interventions on substantively meaningful, sep-
arable components (N and O) of treatment A on Y . If N and O are separable
effects of A, then, in a future randomized trial with six arms:
Figure 23.4
Figure 23.5
1. treat with a = 1
2. treat with a = 0
3. treat with n = 1, o = 1
4. treat with n = 0, o = 0
5. treat with n = 0, o = 1
6. treat with n = 1, o = 0)
then the following two statements are true. First, the mean of the outcome Y
in the first arm equals that in the third and the mean outcome in the second
arm equals that in the fourth. Second, E
Y
n=0,o=1
is identified as the mean
Stensrud et.al. (2021) emphasized
the need for the above equalities of
mean outcomes across arms of the
six-arm trial.
outcome in the fifth arm and E
Y
n=1,o=0
as the mean outcome in the sixth
arm of the future trial, regardless of whether E
Y
n=0,o=1
is not identified
from the observed data.
We can use currently available data on A, M, and Y to identify the sepa-
rable effects of N and O under the assumptions of (i) no unmeasured common
cause of the mediator M and the outcome Y and (ii) no direct effects of the
component O on the mediator M and of component N on outcome Y . In
particular, E
Y
n=0,o=1
equals the mediation formula.
324 Causal mediation
Fine Point 23.2
Separable effects with a surrogate mediator. In the following we adopt the theory of causal diagrams introduced in
Section 9.5. Since the arrow from M to Y is only causally interpretable when there exist well-defined interventions for
the effect of M on Y , the DAG in Figure 23.1 is not causal when those interventions do no exist. That is, M is not a
mediator but rather a surrogate for an unknown variable H that is the true mediator for which well-defined interventions
exist. The causal DAG in Figure 23.4 represents this scenario.
Consider the causal diagram in Figure 23.5, which is an extension of Figure 23.4 with separable components N and
O. In contrast to Figure 23.2, N and Y are not d-separated given M and O in Figure 23.5. Suppose, surprisingly,
we observe that N and Y are independent given M and O in our three-arm trial data. How should we interpret this
observation? There are 4 possibilities: a) we were mistaken: Figure 23.1 rather than 23.4 is the true causal diagram
and M is the true causal mediator, b) M is a one-to-one deterministic function of the true causal mediator H, c)
there is a non-deterministic faithfulness violation in Figure 23.4, and d) N and O are not conditionally independent
but the three-arm trial was too small to detect their dependence. Advocates of causal discovery would tend to adopt
interpretation a) if the sample size in the three-arm trial was large (see Technical Point 10.7).
We now discuss one further reason to prefer an interventionist approach
over earlier approaches to causal mediation. Specifically, it is often the case
that
Figure 23.6
Figure 23.7
Figure 23.8
interventions on the putative mediator M are not well-defined and counter-
factuals like Y
a,m
are then not meaningful. Then neither the pure direct effect
nor the controlled direct effects (described in Technical Point 22.1) based on
M exist. In contrast, the interventionist theory is concerned with effects that
exist, even if interventions on M are not well-defined, as long as substantively
meaningful separable components N and O exist and can be intervened on as
discussed above.
To summarize, an interventionist approach to mediation include the follow-
ing components.
• the hypothesis that treatment A can be decomposed into multiple, sub-
stantially meaningful, separable components, each of which contributes
to the overall effect of treatment and which can, in principle be indepen-
dently intervened on
• the assumptions needed to identify the effects of the separable compo-
nents are, in principle, empirically verifiable in future randomized trials
in which these components are actually intervened on
• well-defined interventions on a purported mediator need not exist
• enhanced communication with subject-matter experts owing to the sub-
stantive specificity of the separable components
• when the identifying assumptions hold, the identifying g-formula is iden-
tical to the mediation formula; however, the identified causal effects refer
to interventions on the separable components.
For simplicity, we considered an example with only two separable components,
but the interventionist framework can accommodate multiple separable com-
ponents of treatment, including those that vary over time.
In this chapter we have reviewed theoretical concepts of mediation, but we
have not emphasized the practical aspects of data analyses to estimate pure
23.4 An interventionist theory of mediation 325
Technical Point 23.3
Path-specific effects and the front door formula. Under Figure 23.6, which is the modified version of Figure 9.14,
the total effect of L on Y is not identified. This is because the contribution of the pathway L → Y to the total effect
cannot be separated from the confounding effect of H. In contrast, under the unmodified causal diagram in Figure 9.14
lacking the L → Y edge, we showed in Fine Point 9.5 that the total effect of L on Y was identified by the front door
formula, as L → A → Y was the sole causal pathway.
We now consider whether the effect of L along the pathway L → A → Y is also identified, and by the same front
door formula when the L → Y edge is present. In the spirit of this chapter, we shall use the substantive story in Fine
Point 9.5 to provide an interventionist formulation of this question. Figure 23.7 is an expanded graph where N records
the value of BMI L reported to the physician responsible for prescribing drug A, and O records the value of L used to
determine referral to physical therapy and diet counseling. The bold arrows indicate a deterministic relationship, since,
in the observed data, we always have L = N = O. Figure 23.8 is a SWIG representing an (unethical) intervention in
which a value n of BMI different from the truth L = N was reported to the physician, but the true value L = O was
used for the referrals. In contrast with earlier in the this chapter, only N has been intervened on. Further, as was our
goal, the effect on Y of the intervention on n is restricted to the path through A. Since L ≡ O even in the intervened
world, we have no need of O. We therefore remove O from Figures 23.7 and 23.8 and again have Y as a child of L.
Then noting trivially that Y
n
⨿ N|L on Figure 23.8, E [Y
n
] should be given by the g-formula based on Figure 23.7
which equals
X
l,a
E [Y |A = a, L = l] Pr[L = l] Pr[A = a|N = n] =
X
a
(
X
l
E [Y |A = a, L = l] pr[L = l]
)
Pr[A = a|L = n]
where the last equality is by the determinism L ≡ N in the data. The right hand side is indeed the front door formula.
However, this derivation is somewhat heuristic due to the presence of null sets arising from determinism. A rigorous
proof is readily obtained by combining determinism with the approach used in Technical Point 21.12 to prove the
front door formula. Note also that, substantively speaking, one generally would not consider N and O as separable
components of L. But that is irrelevant. What matters is that our substantive causal story implies an expanded graph
23.7 containing the new intervention variable N that is deterministically related to L in the actual world (Stensrud et
al., 2023). Wen et al. (2023) have independently and concurrently obtained results essentially equivalent to those of
this technical point. Fulcher et al. (2020) had earlier shown that the above front door formula identifies the cross world
counterfactual quantity E[Y
L,A
l=n
] under the NPSEM-IE model associated with Figure 23.6. Both Wen et al. and this
Technical Point can be seen as interventionist reformulations of Fulcher et al’s result.
direct effects and separable direct effects. In the previous chapter, we adopted
a similar approach when introducing controlled direct effects and principal
stratum direct effects. We hope that our presentation has clarified the scientific
advantages of an interventionist approach to the identification of direct effects.
In the absence of randomized trials with actual interventions on either the
mediator (for controlled direct effects) or components of treatment (for sep-
arable direct effects), all these methodologies rely on observational data and
therefore on the exchangeability assumptions that we have discussed through-
out the book. Hence, valid mediation analyses require adjustment for the
confounders for the effect of treatment and for the effect of the mediator in
addition to other assumptions that we discussed in this chapter. Our causal di-For separable effects, additional is-
sues arise if there is a measured
cause of M and Y that is a child
of N and O (Robins and Richard-
son 2010; Robins et al. 2022).
agram in Figure 23.1 was intended as a teaching device to explore theoretical
issues related to mediation in a simplified setting, not as a realistic repre-
sentation of most studies of causal mediation. In practice, causal mediation
analyses are observational analyses that rely on more heroic assumptions than
non-mediation analyses.
326 References
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Index
accelerated failure time model, 226
administrative end of follow-up,
221
ancillarity, 140
antagonism, 66
as-treated analysis, 302
association, 10
measures, 11
attributable fraction, 40, 68
backdoor criterion, 87
generalized, 255
backdoor path, 85
balancing score, 196
Bayesian interval, 133
bias, 81, 134, 135
amplificatiion, 240
collider, 117
confounding, see confounding
healthy worker, 86, 105
information, see measurement
bias
M-bias, see M-bias
measurement, see
measurement bias
missing data, see missing data
nonresponse, 105
of traditional methods, 263
selection, see selection bias
self-selection, 106
systematic, see systematic
bias
under the alternative, 82
under the null, 82
volunteer, 106
blip function, 287
bootstrapping, 174
bounds for causal effect, 206
natural, 206
sharp, 206
causal DAG, 72, 125
feedback cycles, 262
for time-varying treatments,
251
causal diagrams, 71
augmented, 116
DAG, see causal DAG
signed, 90
twin, 95
causal discovery, 81, 144
causal effect, see effect
censoring, 109, 166, 226
administrative, 221
artificial, 234
as a time-varying treatment,
291
informative, 105
loss to follow-up, 105, 222
channeling, see confounding
cloning, 310
collapsibility, 51, 56
collider, 75, 91, 237
mismeasured, 123
compatibility interval, 136, see
confidence interval
competing event, 114, 222
compliance types, see principal
strata
compositional epistasis, 63
conditionality principle, 138, 139
confidence interval, 132
anticonservative, 133
asymptotic, 133
calibrated, 133
conservative, 133
exact, 133
frequentist, 133
honest, 134
large-sample, 133
of doubly robust machine
learning estimators, 243
small-sample, 133
346 References
valid, 133
Wald, 132
confounder, 90
mismeasured, 122
on causal pathway, 266
surrogate, 94, 129
time-varying, 259
traditional definition, 93, 95
confounding, 12, 82, 85
by indication, 86
strength and direction, 90
structure, 85
time-varying, 260
unmeasured, 88
confounding adjustment, 96
sufficient set, 88, 96
consistency, 4, 33
for censoring, 114
in causal diagrams, 80
sequential, 254, 255
continuity principle, 140
conventional methods, 97
counterfactual outcomes, 4
deterministic, 9
nondeterministic, 10
counterfactual response type, 60
Cox proportional hazards model,
226
cross-fitting, 242
cross-validation, 236, 238
crossover experiment, 16, see
randomized experiment
cumulative incidence, see risk
curse of dimensionality, 142, 159
d-separation, 78
difference-in-differences, 100, 297
direct effect
natural, see pure direct effect
controlled, 305
principal stratum, 306
pure, 306
separable, 321
directed acyclic graph, 71, see
causal DAG
dose-response curve, 149, 164
doubly robust estimator, 175
augmented inverse probability
weighted, 178, 179
based on g-estimation, 192
for time-varying treatments,
280, 284
plug-in, 176
doubly robust machine learning
estimator, 242
effect
average causal effect, 5
conditional, 51
direct, see direct effect
in the compliers, 213, 218
in the treated, 46, 48, 161, 170
in the untreated, 52
individual causal effect, 4, 31
measures, 7
on additive scale, 8
on multiplicative scale, 8
population causal effect, 7
effect modification, 18, 44, 50
additive, 44, 165
in causal diagrams, 83
in marginal structural models,
165
in structural nested models,
288
multiplicative, 44
qualitative, 44
with propensity scores, 200
effect modifier, 44
causal, 46, 84
surrogate, 46, 84
effect-measure modification, 44
estimand, 132
estimate, 9, 132
estimator, 9, 132
closed form, 190, 290
consistent, 9, 132, 135
doubly robust, see doubly
robust estimator
exactly unbiased, 135
Fisher consistent, 151
nonparametric, 150
parametric, 149
systematically biased, 135
etiologic fraction, 40
excess fraction, 40, 68
exchangeability, 14, 29
and confounding, 87
conditional, 18, 30
expressed parametrically, 182
for censoring, 113
full, 15
in causal diagrams, 72
marginal, 18
mean, 15
partial, 48
References 347
sequential, see sequential
exchangeability
exclusion restriction, 204, 215, 300
exogeneity, 14, 105
experimental treatment
assumption, see
positivity
exposure, see treatment
faithfulness, 79
finest causally interpreted
structural tree graph, 73
FFRCISTG, 74, 88
frailty, 108
front door criterion, 101
front door formula, 101, 295, 296
functional form, 149
g-computation, see g-formula
g-computation algorithm formula,
see g-formula
g-estimation, 187, 192
for survival analysis, 231
for time-varying treatments,
283
g-formula, 101
as a simulation, 272
big, 294
for a density, 275
for survival analysis, 230
for time-varying treatments,
271
front door formula, 295
general expression, 275
ICE, 285
mediation formula, 320
parametric, 175, 274
plug-in, 175, 274
representations, 285
g-methods, 97, 271
g-null paradox, 280
g-null test, 264
grace period, 311
Hajek estimator, 160
hazard, 223
discrete time, 223
hazard ratio, 223
built-in selection bias, 225
via a logistic model, 227
via a proportional hazards
model, 225
heterogeneity of treatment effects,
see effect modification
hidden variable, 126
homogeneity in IV estimation, 208
homoscedasticity, 149
Horvitz-Thompson estimator, 160
identifiability, 27, 29
conditions, 28
nonparametric, 29
identification, 131
partial, 206
ignorability, 28, 105
independence, 11
conditional, 76
cross-world, 88, 319
mean independence, 11
instrument, 203
bias amplification, 240
candidate, 205
causal, 204
surrogate, 204
weak, 205, 215
instrumental conditions, 203, 204,
214
falsification tests for, 205
instrumental variable, see
instrument
instrumental variable estimation,
206, 314
additive structural mean
models, 209
multiplicative structural mean
models, 210
usual estimand, 207
Wald estimator, 207
intention-to-treat analysis, 300
modified, 301
pseudo-, 301
intention-to-treat effect, 300, 304
observational analog, 308
interaction, 57
additive, 57
biologic, see sufficient cause
interaction
in causal diagrams, 84
multiplicative, 59
subadditive, 59
submultiplicative, 59
sufficient cause, 65
superadditive, 59
supermultiplicative, 59
interference, 5, 50
intervention, see treatment
joint, 57
348 References
sufficiently well-defined, 35,
80, 114, 125, 312
inverse probability weighting
augmented, 179
inverse probability weighting, 22
augmented, 178
for censoring, 167, 292
for survival analysis, 228
for time-varying treatments,
276
nonstabilized, 158, 276, 277
stabilized, 161, 167, 168, 276,
277
vs. standardization, 173
with models, 158
iterated conditional expectation,
see g-formula ICE
Kaplan-Meier curve, 224, 226
karma, see treatment
kernel function, 155
lasso regression, 236
least squares
ordinary, 149, 279
two-stage, 207
weighted, 159, 279
link function, 155
linkage disequilibrium, 86
local average treatment effect, see
effect in the compliers
M-bias, 91, 105, 239, 274
machine learning algorithms, 241
Mantel-Haenszel method, 53
marginal structural model, 163
faux, 166, 193
for the mean, 163
for time-varying treatments,
278
logistic, 165
semiparametric, 184
vs. structural nested model,
184, 288
matching, 51, 79
with propensity scores, 198
measurement bias, 82
strength and direction, 122
measurement error, 119
independent, 120, 121
nondifferential, 120, 121
mediation formula, 318
and the g-formula, 320
mediator, 76, 239, 305
Mendelian randomization, 205
misclassification, 120
missing data, 18, 105, 166
model, 149
for the mean outcome, 171
generalized additive, 155
linear, 149
marginal structural, see
marginal structural
model
misspecification, 150
multiplicative survival, 116
parametric, 149
parsimonious, 151
predictive, 200
rank-preserving, 186
saturated, 150
semiparametric, 155, 183, 226
structural, 199
structural nested, see
structural nested model
monotonicity, 62, 303
in IV estimation, 211, 218
multiply robust estimator, 283,
284
negative outcome controls, 100
nonparametric structural equation
model, 73
NPSEM-IE, 74, 88
nuisance parameter, 194
null hypothesis
of no average causal effect, 5,
44
sharp causal null, 6, 44, 186
null preservation, 164, 190, 301
number needed to treat, 8
observational study, 27, 72
ommitted variable bias, 105
on-treatment analysis, 302
outcome regression, 193
overadjustment for mediators, 239
overfitting, 238
per protocol analysis, 302
per-protocol effect, 300, 304
observational analog, 308
placebo, 300
placebo controls, see negative
outcome controls
plan, see treatment strategy
point estimate, see estimate
References 349
policy, see treatment, see
treatment strategy
pooling, 53
population stratification, 86
posible worlds, 37
positivity, 25, 32
for censoring, 113
for g-formula, 272
for propensity score, 196, 198
in causal diagrams, 78
sequential, 254, 255
structural, 170
violations, 163
potential outcomes, see
counterfactual outcomes
pragmatic trial, 303
predicted value, 149
predictive algorithm, 236
black-box, 236
interpretable, 236
principal strata, 211
prognostic score, 196
propensity score, 97, 159, 195
proximal causal inference, 100
pseudo-population, 22, 158, 161
pure direct effect, 317
random error, 10
random variability, 8
randomization, 13
conditional, 17
randomization-based inference,
135
randomized experiment, 13
conditionally randomized, 17,
30, 72
crossover, 31
double-blind, 203, 300
ideal, 14
marginally randomized, 17,
29, 72
placebo-controlled, 203, 300
sequentially, 253
rank preservation, 185, 286
additive, 186
local, 286
regime, see treatment strategy
regression discontinuity design,
219
relevance condition in IV
estimation, 204, 214
residual, 149
restriction, 51
reverse causation, 86
ridge regression, 236
risk, 223
robust variance, 160, 279
sample splitting, 242
sampling variability, 9, 134
selection bias, 103
in case-control studies, 106
in hazard ratios, 108
strength and direction, 117
structure, 103
under the alternative, 82, 238
under the null, 82, 103, 237
selection on observables, 105
selection on unobservables, 107
selection without bias, 115
sensitivity analysis, 177, 245
for model misspecification,
154
for selection bias, 158
for unmeasured confounding,
90
in instrumental variable
estimation, 217
using g-estimation, 189
sequential emulation, 310
sequential exchangeability, 254,
256
full, 256
static, 257
unconditional, 254
shrinkage methods, 237
Simpson’s paradox, 109
single-world intervention graphs,
see SWIG
smoothing, 151, 225
stable-unit-treatment-value
assumption, see SUTVA
standard error, 132
standardization, 20
vs. inverse probability
weighting, 173
of the mean outcome, 172
with models, 169
with propensity scores, 197
stratification, 18
as a form of adjustment, 49
bias for time-varying
treatments, 265
to identify effect modification,
45
with propensity scores, 197
350 References
structural nested model, 183
accelerated failure time
model, 231
cumulative failure time
model, 231, 232
cumulative survival time
model, 231, 232
logistic, 185
mean model, 183, 284
multiplicative, 185
saturated, 287
vs. marginal structural
model, 184, 288
with two or more parameters,
190
sufficient cause, 62
sufficient-component cause, 63
super-population, 9, 132, 137
survival analysis, 221
models, 226
with time-varying treatments,
293
SUTVA, 5, 6
SWIG, 95
arrows from intervention
nodes, 258
for time-varying treatments,
255
synergism, 66
systematic bias, 81, 135, 136
target experiment, see target trial
target trial, 39
emulation, 307
protocol components, 307
with sustained strategies, 303
targeted maximum likelihood
estimation, see TMLE
targeted minimum loss-based
estimation, see TMLE
time zero, 309
TMLE, 179, 281, 283
total indirect effect, 318
transportability, 48, 50
treatment, 3
history, 249, 274
mismeasured, 269
multiple versions, 6, 34, 50
natural value of, 96
strategy, see treatment
strategy
time-varying, 249
treatment strategy, 250
deterministic, 251
dynamic, 250, 252, 278
optimal, 251
random, 251
static, 251
treatment variation irrelevance, 6
treatment-confounder feedback,
261
variable selection, 235
in regression models, 237
